a single case study intervention

Single-Case Design, Analysis, and Quality Assessment for Intervention Research

Affiliation.

• 1 Biomechanics & Movement Science Program, Department of Physical Therapy, University of Delaware, Newark, Delaware (M.A.L., A.B.C., I.B.); and Division of Educational Psychology & Methodology, State University of New York at Albany, Albany, New York (M.M.).
• PMID: 28628553
• PMCID: PMC5492992
• DOI: 10.1097/NPT.0000000000000187

Background and purpose: The purpose of this article is to describe single-case studies and contrast them with case studies and randomized clinical trials. We highlight current research designs, analysis techniques, and quality appraisal tools relevant for single-case rehabilitation research.

Summary of key points: Single-case studies can provide a viable alternative to large group studies such as randomized clinical trials. Single-case studies involve repeated measures and manipulation of an independent variable. They can be designed to have strong internal validity for assessing causal relationships between interventions and outcomes, as well as external validity for generalizability of results, particularly when the study designs incorporate replication, randomization, and multiple participants. Single-case studies should not be confused with case studies/series (ie, case reports), which are reports of clinical management of a patient or a small series of patients.

Recommendations for clinical practice: When rigorously designed, single-case studies can be particularly useful experimental designs in a variety of situations, such as when research resources are limited, studied conditions have low incidences, or when examining effects of novel or expensive interventions. Readers will be directed to examples from the published literature in which these techniques have been discussed, evaluated for quality, and implemented.

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In This Article Expand or collapse the "in this article" section Single-Case Experimental Designs

Introduction, general overviews and primary textbooks.

• Textbooks in Applied Behavior Analysis
• Types of Single-Case Experimental Designs
• Model Building and Randomization in Single-Case Experimental Designs
• Visual Analysis of Single-Case Experimental Designs
• Effect Size Estimates in Single-Case Experimental Designs
• Reporting Single-Case Design Intervention Research

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Single-Case Experimental Designs by S. Andrew Garbacz , Thomas R. Kratochwill LAST MODIFIED: 29 July 2020 DOI: 10.1093/obo/9780199828340-0265

Single-case experimental designs are a family of experimental designs that are characterized by researcher manipulation of an independent variable and repeated measurement of a dependent variable before (i.e., baseline) and after (i.e., intervention phase) introducing the independent variable. In single-case experimental designs a case is the unit of intervention and analysis (e.g., a child, a school). Because measurement within each case is conducted before and after manipulation of the independent variable, the case typically serves as its own control. Experimental variants of single-case designs provide a basis for determining a causal relation by replication of the intervention through (a) introducing and withdrawing the independent variable, (b) manipulating the independent variable across different phases, and (c) introducing the independent variable in a staggered fashion across different points in time. Due to their economy of resources, single-case designs may be useful during development activities and allow for rapid replication across studies.

Several sources provide overviews of single-case experimental designs. Barlow, et al. 2009 includes an overview for the development of single-case experimental designs, describes key considerations for designing and conducting single-case experimental design research, and reviews procedural elements, assessment strategies, and replication considerations. Kazdin 2011 provides detailed coverage of single-case experimental design variants as well as approaches for evaluating data in single-case experimental designs. Kratochwill and Levin 2014 describes key methodological features that underlie single-case experimental designs, including philosophical and statistical foundations and data evaluation. Ledford and Gast 2018 covers research conceptualization and writing, design variants within single-case experimental design, definitions of variables and associated measurement, and approaches to organize and evaluate data. Riley-Tillman and Burns 2009 provides a practical orientation to single-case experimental designs to facilitate uptake and use in applied settings.

Barlow, D. H., M. K. Nock, and M. Hersen, eds. 2009. Single case experimental designs: Strategies for studying behavior change . 3d ed. New York: Pearson.

A comprehensive reference about the process of designing and conducting single-case experimental design studies. Chapters are integrative but can stand alone.

Kazdin, A. E. 2011. Single-case research designs: Methods for clinical and applied settings . 2d ed. New York: Oxford Univ. Press.

A complete overview and description of single-case experimental design variants as well as information about data evaluation.

Kratochwill, T. R., and J. R. Levin, eds. 2014. Single-case intervention research: Methodological and statistical advances . New York: Routledge.

The authors describe in depth the methodological and analytic considerations necessary for designing and conducting research that uses a single-case experimental design. In addition, the text includes chapters from leaders in psychology and education who provide critical perspectives about the use of single-case experimental designs.

Ledford, J. R., and D. L. Gast, eds. 2018. Single case research methodology: Applications in special education and behavioral sciences . New York: Routledge.

Covers the research process from writing literature reviews, to designing, conducting, and evaluating single-case experimental design studies.

Riley-Tillman, T. C., and M. K. Burns. 2009. Evaluating education interventions: Single-case design for measuring response to intervention . New York: Guilford Press.

Focuses on accelerating uptake and use of single-case experimental designs in applied settings. This book provides a practical, “nuts and bolts” orientation to conducting single-case experimental design research.

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• Published: 22 November 2022

Single case studies are a powerful tool for developing, testing and extending theories

• Lyndsey Nickels   ORCID: orcid.org/0000-0002-0311-3524 1 , 2 ,
• Simon Fischer-Baum   ORCID: orcid.org/0000-0002-6067-0538 3 &
• Wendy Best   ORCID: orcid.org/0000-0001-8375-5916 4  

Nature Reviews Psychology volume  1 ,  pages 733–747 ( 2022 ) Cite this article

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Psychology embraces a diverse range of methodologies. However, most rely on averaging group data to draw conclusions. In this Perspective, we argue that single case methodology is a valuable tool for developing and extending psychological theories. We stress the importance of single case and case series research, drawing on classic and contemporary cases in which cognitive and perceptual deficits provide insights into typical cognitive processes in domains such as memory, delusions, reading and face perception. We unpack the key features of single case methodology, describe its strengths, its value in adjudicating between theories, and outline its benefits for a better understanding of deficits and hence more appropriate interventions. The unique insights that single case studies have provided illustrate the value of in-depth investigation within an individual. Single case methodology has an important place in the psychologist’s toolkit and it should be valued as a primary research tool.

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The authors thank all of those pioneers of and advocates for single case study research who have mentored, inspired and encouraged us over the years, and the many other colleagues with whom we have discussed these issues.

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Nickels, L., Fischer-Baum, S. & Best, W. Single case studies are a powerful tool for developing, testing and extending theories. Nat Rev Psychol 1 , 733–747 (2022). https://doi.org/10.1038/s44159-022-00127-y

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Optimizing behavioral health interventions with single-case designs: from development to dissemination

Jesse dallery.

Department of Psychology, University of Florida, P. O. box 112250, Gainesville, FL 32611 USA

Bethany R Raiff

Department of Psychology, Rowan University, Glassboro, USA

Over the past 70 years, single-case design (SCD) research has evolved to include a broad array of methodological and analytic advances. In this article, we describe some of these advances and discuss how SCDs can be used to optimize behavioral health interventions. Specifically, we discuss how parametric analysis, component analysis, and systematic replications can be used to optimize interventions. We also describe how SCDs can address other features of optimization, which include establishing generality and enabling personalized behavioral medicine. Throughout, we highlight how SCDs can be used during both the development and dissemination stages of behavioral health interventions.

Research methods are tools to discover new phenomena, test theories, and evaluate interventions. Many researchers have argued that our research tools have become limited, particularly in the domain of behavioral health interventions [ 1 – 9 ]. The reasons for their arguments vary, but include an overreliance on randomized controlled trials, the slow pace and high cost of such trials, and the lack of attention to individual differences. In addition, advances in mobile and sensor-based data collection now permit real-time, continuous observation of behavior and symptoms over extended durations [ 3 , 10 , 11 ]. Such fine-grained observation can lead to tailoring of treatment based on changes in behavior, which is challenging to evaluate with traditional methods such as a randomized trial.

In light of the limitations of traditional designs and advances in data collection methods, a growing number of researchers have advocated for alternative research designs [ 2 , 7 , 10 ]. Specifically, one family of research designs, known as single-case designs (SCDs), has been proposed as a useful way to establish the preliminary efficacy of health interventions [ 3 ]. In the present article, we recapitulate and expand on this proposal, and argue that they can be used to optimize health interventions.

We begin with a description of what we consider to be a set of criteria, or ideals, for what research designs should accomplish in attempting to optimize an intervention. Admittedly, these criteria are self-serving in the sense that most of them constitute the strengths of SCDs, but they also apply to other research designs discussed in this volume. Next, we introduce SCDs and how they can be used to optimize treatment using parametric and component analyses. We also describe how SCDs can address other features of optimization, which include establishing generality and enabling personalized behavioral medicine. Throughout, we also highlight how these designs can be used during both the development and dissemination of behavioral health interventions. Finally, we evaluate the extent to which SCDs live up to our ideals.

AN OPTIMIZATION IDEAL

During development and testing of a new intervention, our methods should be efficient, flexible, and rigorous. We would like efficient methods to help us establish preliminary efficacy, or “clinically significant patient improvement over the course of treatment” [ 12 ] (p. 137). We also need flexible methods to test different parameters or components of an intervention. Just as different doses of a drug treatment may need to be titrated to optimize effects, different parameters or components of a behavioral treatment may need to be titrated to optimize effects. It should go without saying that we also want our methods to be rigorous, and therefore eliminate or reduce threats to internal validity.

Also, during development, we would like methods that allow us to assess replications of effects to establish the reliability and generality of an intervention. Replications, if done systematically and thoughtfully, can answer questions about for whom and under what conditions an intervention is effective. Answering these questions speaks to the generality of research findings. As Cohen [ 13 ] noted in a seminal article: “For generalization, psychologists must finally rely, as has been done in all the older sciences, on replication” (p. 997). Relying on replications and establishing the conditions under which an intervention works could also lead to more targeted, efficient dissemination efforts.

During dissemination, when an intervention is implemented in clinical practice, we again would like to know if the intervention is producing a reliable change in behavior for a particular individual. (Here, “we” may refer to practitioners in addition to researchers.) With knowledge derived from development and efficacy testing, we may be able to alter components of an intervention that impact its effectiveness. But, ideally, we would like to not only alter but verify whether these components are working. Also, recognizing that behavior change is idiosyncratic and dynamic, we may need methods that allow ongoing tailoring and testing. This may result in a kind of personalized behavioral medicine in which what gets personalized, and when, is determined through experimental analysis.

In addition, during both development and dissemination, we want methods that afford innovation. We should have methods that allow rapid, rigorous testing of new treatments, and which permit incorporating new technologies to assess and treat behavior as they become available. This might be thought of as systematic play. Whatever we call it, it is a hallmark of the experimental attitude in science.

INTRODUCTION TO SINGLE-CASE DESIGNS

SCDs include an array of methods in which each participant, or case, serves as his or her own control. Although these methods are conceptually rooted in the study of cognition and behavior [ 14 ], they are theory-neutral and can be applied to any health intervention. In a typical study, some behavior or symptom is measured repeatedly during all conditions for all participants. The experimenter systematically introduces and withdraws control and intervention conditions, and assesses effects of the intervention on behavior across replications of these conditions within and across participants. Thus, these studies include repeated, frequent assessment of behavior, experimental manipulation of the independent variable (the intervention or components of the intervention), and replication of effects within and across participants.

The main challenge in conducting a single-case experiment is collecting data of the same behavior or symptom repeatedly over time. In other words, a time series must be possible. If behavior or symptoms cannot be assessed frequently, then SCDs cannot be used (e.g., on a weekly basis, at a minimum, for most health interventions). Fortunately, technology is revolutionizing methods to collect data. For example, ecological momentary assessment (EMA) enables frequent input by an end-user into a handheld computer or mobile phone [ 15 ]. Such input occurs in naturalistic settings, and it usually occurs on a daily basis for several weeks to months. EMA can therefore reveal behavioral variation over time and across contexts, and it can document effects of an intervention on an individual’s behavior [ 15 ]. Sensors to record physical activity, medication adherence, and recent drug use also enable the kind of assessment required for single-case research [ 10 , 16 ]. In addition, advances in information technology and mobile phones can permit frequent assessment of behavior or symptoms [ 17 , 18 ]. Thus, SCDs can capitalize on the ability of technology to easily, unobtrusively, and repeatedly assess health behavior [ 3 , 18 , 19 ].

SCDs suffer from several misconceptions that may limit their use [ 20 – 23 ]. First, a single case does not mean “ n of 1.” The number of participants in a typical study is almost always more than 1, usually around 6 but sometimes as many as 20, 40, or more participants [ 24 , 25 ]. Also, the unit of analysis, or “case,” could be individual participants, clinics, group homes, hospitals, health care agencies, or communities [ 1 ]. Given that the unit of analysis is each case (i.e., participant), a single study could be conceptualized as a series of single-case experiments. Perhaps a better label for these designs would be “intrasubject replication designs” [ 26 ]. Second, SCDs are not limited to interventions that produce large, immediate changes in behavior. They can be used to detect small but meaningful changes in behavior and to assess behavior that may change slowly over time (e.g., learning a new skill) [ 27 ]. Third, SCDs are not quasi-experimental designs [ 20 ]. The conventional notions that detecting causal relations requires random assignment and/or random sampling are false [ 26 ]. Single-case experiments are fully experimental and include controls and replications to permit crisp statements about causal relations between independent and dependent variables.

VARIETIES OF SINGLE-CASE DESIGNS

The most relevant SCDs to behavioral health interventions are presented in Table  1 . The table also presents some procedural information and advantages and disadvantages for each design. (The material below is adapted from [ 3 ]) There are also a number of variants of these designs, enabling flexibility in tailoring the design based on practical or empirical considerations [ 27 , 28 ]. For example, there are several variants to circumvent long periods of assessing behavior during baseline conditions, which may be problematic if the behavior is dangerous, before introducing a potentially effective intervention [ 28 ].

Several single-case designs, including general procedures, advantages, and disadvantages

Procedural controls must be in place to make inferences about causal relations, such as clear, operational definitions of the dependent variables, reliable and valid techniques to assess the behavior, and the experimental design must be sufficient to rule out alternative hypotheses for the behavior change. Table  2 presents a summary of methodological and assessment standards to permit conclusions about treatment effects [ 29 , 30 ]. These standards were derived from Horner et al. [ 29 ] and from the recently released What Works Clearinghouse (WWC) pilot standards for evaluating single-case research to inform policy and practice (hereafter referred to as the SCD standards) [ 31 ].

Quality indicators for single-case research [ 29 ]

All of the designs listed in Table  1 entail a baseline period of observation. During this period, the dependent variable is measured repeatedly under control conditions. For example, Dallery, Glenn, and Raiff [ 24 ] used a reversal design to assess effects of an internet-based incentive program to promote smoking cessation, and the baseline phase included self-monitoring, carbon monoxide assessment of smoking status via a web camera, and monetary incentives for submitting videos. The active ingredient in the intervention, incentives contingent on objectively verified smoking abstinence, was not introduced until the treatment phase.

The duration of the baseline and the pattern of the data should be sufficient to predict future behavior. That is, the level of the dependent variable should be stable enough to predict its direction if the treatment was not introduced. If there is a trend in the direction of the anticipated treatment effect during baseline, or if there is too much variability, the ability to detect a treatment effect will be compromised. Thus, stability, or in some cases a trend in the direction opposite the predicted treatment effect, is desirable during baseline conditions.

In some cases, the source(s) of variability can be identified and potentially mitigated (e.g., variability could be reduced by automating data collection, standardizing the setting and time for data collection). However, there may be instances when there is too much variability during baseline conditions, and thus, detecting a treatment effect will not be feasible. There are no absolute standards to define what “too much” variability means [ 27 ]. Excessive variability is a relative term, which is typically determined by a comparison of performance within and between conditions (e.g., between baseline and intervention conditions) in a single-case experiment. The mere presence of variability does not mean that a single-case approach should be abandoned, however. Indeed, identifying the sources of variability and/or assessing new measurement strategies can be evaluated using SCDs. Under these conditions, the outcome of interest is not an increase or a decrease in some behavior or symptom but a reduction in variability. Once accomplished, the researcher has not only learned something useful but is also better prepared to evaluate the effects of an intervention to increase or decrease some health behavior.

REVERSAL DESIGNS

In a reversal design, a treatment is introduced after the baseline period, and then a baseline period is re-introduced, hence, the “reversal” in this design (also known as an ABA design, where “A” is baseline and “B” is treatment). Using only two conditions, such as a pre-post design, is not considered sufficient to demonstrate experimental control because other sources of influence on behavior cannot be ruled out [ 31 , 32 ]. For example, a smoking cessation intervention could coincide with a price increase in cigarettes. By returning to baseline conditions, we could assess and possibly rule out the influence of the price increase on smoking. Researchers also often use a reversal to the treatment condition. Thus, the experiment ends during a treatment period (an ABAB design). Not only is this desirable from the participant’s perspective but it also provides a replication of the main variable of interest—the treatment [ 33 ].

Figure  1 displays an idealized, ABAB reversal design, and each panel shows data from a different participant. Although all participants were exposed to the same four conditions, the duration of the conditions differed because of trends in the conditions. For example, for participant 1, the beginning of the first baseline condition displays a consistent downward trend (in the same direction as the expected text-message treatment effects). If we were to introduce the smoking cessation-related texts after only five or six baseline sessions, it would be unclear if the decrease in smoking was a function of the independent variable. Therefore, continuing the baseline condition until there is no visible trend helps build our confidence about the causal role of the treatment when it is introduced. The immediate decrease in the level of smoking for participant 1 when the treatment is introduced also implicates the treatment. We can also detect, however, an increasing trend in the early portion of the treatment condition. Thus, we need to continue the treatment condition until there is no undesirable trend before returning to the baseline condition. Similar patterns can be seen for participants 2–4. Based on visual analysis of Fig.  1 , we would conclude that treatment is exerting a reliable effect on smoking. But, the meaningfulness of this effect requires additional considerations (see the section below on “ Visual, Statistical, and Social Validity Analysis ”).

Example of a reversal design showing experimental control and replications within and between subjects. Each panel represents a different participant, each of whom experienced two baseline and two treatment conditions

Studies using reversal designs typically include at least four or more participants. The goal is to generate enough replications, both within participants and across participants, to permit a confident statement about causal relations. For example, several studies on incentive-based treatment to promote drug abstinence have used 20 participants in a reversal design [ 24 , 25 ]. According to the SCD standards, there must be a minimum of three replications to support conclusions about experimental control and thus causation. Also, according to the SCD standards, there must be at least three and preferably five data points per phase to allow the researcher to evaluate stability and experimental effects [ 31 ].

There are two potential limitations of reversal designs in the context of behavioral health interventions. First, the treatment must be withdrawn to demonstrate causal relations. Some have raised an ethical objection about this practice [ 11 ]. However, we think that the benefits of demonstrating that a treatment works outweigh the risks of temporarily withdrawing treatment (in most cases). The treatment can also be re-instituted in a reversal design (i.e., an ABAB design). Second, if the intervention produces relatively permanent changes in behavior, then a reversal to pre-intervention conditions may not be possible. For example, a treatment that develops new skills may imply that these skills cannot be “reversed.” Some interventions do not produce permanent change and must remain in effect for behavior change to be maintained, such as some medications and incentive-based procedures. Under conditions where behavior may not return to baseline levels when treatment is withdrawn, alternative designs, such as multiple-baseline designs, should be used.

MULTIPLE-BASELINE DESIGNS

In a multiple-baseline design, the durations of the baselines vary systematically for each participant in a so-called staggered fashion. For example, one participant may start treatment after five baseline days, another after seven baseline days, then nine, and so on. After baseline, treatment is introduced, and it remains until the end of the experiment (i.e., there are no reversals). Like all SCDs, this design can be applied to individual participants, clusters of individuals, health care agencies, and communities. These designs are also referred to as interrupted time-series designs [ 1 ] and stepped wedge designs [ 7 ].

The utility of these designs is derived from demonstrating that change occurs when, and only when, the intervention is directed at a particular participant (or whatever the unit of analysis happens to be [ 28 ]). The influence of other factors, such as idiosyncratic experiences of the individual or self-monitoring (e.g., reactivity), can be ruled out by replicating the effect across multiple individuals. A key to ruling out extraneous factors is a stable enough baseline phase (either no trends or a trend in the opposite direction to the treatment effect). As replications are observed across individuals, and behavior changes when and only when treatment is introduced, confidence that behavior change was caused by the treatment increases.

As noted above, multiple-baseline designs are useful for interventions that teach new skills, where behavior would not be expected to “reverse” to baseline levels. Multiple-baseline designs also obviate the ethical concern about withdrawing treatment (as in a reversal design) or using a placebo control comparison group (as in randomized trials), as all participants are exposed to the treatment with multiple-baseline designs.

Figure  2 illustrates a simple, two-condition multiple-baseline design replicated across four participants. As noted above, the experimenter should introduce treatment only when the data appear stable during baseline conditions. The durations of the baseline conditions are staggered for each participant, and the dependent variable increases when, and only when, the independent variable is introduced for all participants. The SCD standards requires at least six phases (i.e., three baseline and three treatment) with at least five data points per phase [ 31 ]. Figure  2 suggests reliable increases in behavior and that the treatment was responsible for these changes.

Example of a multiple-baseline design showing experimental control and replications between subjects. Each row represents a different participant, each of whom experienced a baseline and treatment. The baseline durations differed across participants

CHANGING CRITERION DESIGN

The changing criterion design is also relevant to optimizing interventions [ 34 ]. In a changing criterion design, a baseline is conducted until stability is attained. Then, a treatment goal is introduced, and goals are made progressively more difficult. Behavior should track the introduction of each goal, thus demonstrating control by the level of the independent variable [ 28 ]. For example, Kurti and Dallery [ 35 ] used a changing criterion design to increase activity in six sedentary adults using an internet-based contingency management program to promote walking. Weekly step count goals were gradually increased across 5-day blocks. The step counts for all six participants increased reliably with each increase in the goals, thereby demonstrating experimental control of the intervention. This design has many of the same benefits of the multiple-baseline design, namely that a reversal is not required for ethical or potentially practical reasons (i.e., irreversible treatment effects).

VISUAL, STATISTICAL, AND SOCIAL VALIDITY ANALYSIS

Analyzing the data from SCDs involves three questions: (a) Is there a reliable effect of the intervention? (b) What is the magnitude of the effect? and (c) Are the results clinically meaningful and socially valid [ 31 ]? Social validity refers to the extent to which the goals, procedures, and results of an intervention are socially acceptable to the client, the researcher or health care practitioner, and society [ 36 – 39 ]. The first two questions can be answered by visual and statistical analysis, whereas the third question requires additional considerations.

The SCD standards prioritizes visual analysis of the time-series data to assess the reliability and magnitude of intervention effects [ 29 , 31 , 40 ]. Clinically significant change in patient behavior should be visible. Visual analysis prioritizes clinically significant change in health-related behavior as opposed to statistically significant change in group behavior [ 13 , 41 , 42 ]. Although several researchers have argued that visual analysis may be prone to elevated rates of type 1 error, such errors may be limited to a narrow range of conditions (e.g., when graphs do not contain contextual information about the nature of the plotted behavioral data) [ 27 , 43 ]. Furthermore, in recent years, training in visual analysis has become more formalized and rigorous [ 44 ]. Perhaps as a result, Kahng and colleagues found high reliability among visual analysts in judging treatment effects based on analysis of 36 ABAB graphs [ 45 ]. The SCD standards recommends four steps and the evaluation of six features of the graphical displays for all participants in a study, which are displayed in Table  3 [ 31 ]. As the visual analyst progresses through the steps, he or she also uses the six features to evaluate effects within and across experimental phases.

Four steps and six outcome measures to evaluate when conducting visual analysis of time-series data

In addition to visual analysis, several regression-based approaches are available to analyze time-series data, such as autoregressive models, robust regression, and hierarchical linear modeling (HLM) [ 46 – 49 ]. A variety of non-parametric statistics are also available [ 27 ]. Perhaps because of the proliferation of statistical methods, there is a lack of consensus about which methods are most appropriate in light of different properties of the data (e.g., the presence of trends and autocorrelation [ 43 , 50 ], the number of data points collected, etc.). A discussion of statistical techniques is beyond the scope of this paper. We recommend Kazdin’s [ 27 ] or Barlow and colleague’s [ 28 ] textbooks as useful resources regarding statistical analysis of time-series data. The SCD standards also includes a useful discussion of statistical approaches for data analysis [ 31 ].

A variety of effect size calculations have been proposed for SCDs [ 13 , 51 – 54 ]. Although effect size estimates may allow for rank ordering of most to least effective treatments [ 55 ], most estimates do not provide metrics that are comparable to effect sizes derived from group designs [ 31 ]. However, one estimate that provides metrics comparable to group designs has been developed and tested by Shadish and colleagues [ 56 , 57 ]. They describe a standardized mean difference statistic ( d ) that is equivalent to the more conventional d in between-groups experiments. The d statistic can also be used to compute power based on the number of observations in each condition and the number of cases in an experiment [ 57 ]. In addition, advances in effect size estimates has led to several meta-analyses of results from SCDs [ 48 , 58 – 61 ]. Zucker and associates [ 62 ] explored Bayesian mixed-model strategy to combining SCDs using, which allowed population-level claims about the merits of different intervention strategies.

Determining whether the results are clinically meaningful and socially valid can be informed by visual and most forms of statistical analysis (i.e., not null-hypothesis significance testing) [ 42 , 63 ]. One element in judging social validity concerns the clinical meaningfulness of the magnitude of behavior change. This judgment can be made by the researcher or clinician in light of knowledge of the subject matter, and perhaps by the client being treated. Depending on factors such as the type of behavior and the way in which change is measured, the judgment can also be informed by previous research on a minimal clinically important difference (MCID) for the behavior or symptom under study [ 64 , 65 ]. The procedures used to generate the effect also require consideration. Intrusive procedures may be efficacious yet not acceptable. The social validity of results and procedures should be explicitly assessed when conducting SCD research, and a variety of tools have emerged to facilitate such efforts [ 37 ]. Social validity assessment should also be viewed as a process [ 37 ]. That is, it can and should be assessed at various time points as an intervention is developed, refined, and eventually implemented. Social validity may change as the procedures and results of an intervention are improved and better appreciated in the society at large.

OPTIMIZATION METHODS AND SINGLE-CASE DESIGNS

The SCDs described above provide an efficient way to evaluate the effects of a behavioral intervention. However, in most of the examples above, the interventions were held constant during treatment periods; that is, they were procedurally static (cf. [ 35 ]). This is similar to a randomized trial, in which all components of an intervention are delivered all at once and held constant throughout the study. However, the major difference between the examples above and traditional randomized trials is efficiency: SCDs usually require less time and fewer resources to demonstrate that an intervention can change behavior. Nevertheless, a single, procedurally static single-case experiment does not optimize treatment beyond showing whether or not it works.

One way to make initial efficacy testing more dynamic would be to conduct a series of single-case experiments in which aspects of the treatment are systematically explored. For example, a researcher could assess effects of different frequencies, timings, or tailoring dimensions of a text-based intervention to promote physical activity. Such manipulation could also be conducted in separate experiments conducted by the same or different researchers. Some experiments may reveal larger effects than others, which could then lead to further replications of the effects of the more promising intervention elements. This iterative development process, with a focus on systematic manipulation of treatment elements and replications of effects within and across experiments, could lead to an improved intervention within a few years’ time. Arguably, this process could yield more clinically useful information than a procedurally static randomized trial conducted over the same period [ 5 , 17 ].

To further increase the efficiency of optimizing treatment, different components or parameters of an intervention can be systematically evaluated within and across single-case experiments. There are two ways to optimize treatment using these methods: parametric and component analyses.

PARAMETRIC ANALYSIS

Parametric analysis involves exposing participants to a range of values of the independent variable, as opposed to just one or two values. To qualify as a parametric analysis, three is the minimum number of values that must be evaluated, as this number is the minimum to evaluate the function form relating the independent to the dependent variable. One goal of a parametric analysis is to identify the optimal value that produces a behavioral outcome. Another goal is to identify general patterns of behavior engendered by a range of values of the independent variable [ 26 , 63 ].

Many behavioral health interventions can be delivered at different levels [ 66 ] and are therefore amenable to parametric analysis. For example, text-based prompts can be delivered at different frequencies, incentives can be delivered at different magnitudes and frequencies, physical activity can occur at different frequencies and intensities, engagement in a web-based program can occur at different levels, medications can be administered at different doses and frequencies, and all of the interventions could be delivered for different durations.

The repeated measures, and resulting time-series data, that are inherent to all SCDs (e.g., reversal and multiple-baseline designs) make them useful designs to conduct parametric analyses. For example, two doses of a medication, low versus high, labeled B and C, respectively, could be assessed using a reversal design [ 67 ]. There may be several possible sequences to conduct the assessment such as ABCBCA or ABCABCA. If C is found to be more effective of the two, it might behoove the researcher to replicate this condition using an ABCBCAC design. A multiple baseline across participants could also be conducted to assess the two doses, one dose for each participant, but this approach may be complicated by individual variability in medication effects. Instead, the multiple-baseline approach could be used on a within-subject basis, where the durations of not just the baselines but of the different dose conditions are varied across participants [ 68 ].

Guyatt and colleagues [ 5 ] provide an excellent discussion about how parametric analysis can be used to optimize an intervention. The intervention was amitriptyline for the treatment of fibrositis. The logic and implications of the research tactics, however, also apply to other interventions that have parametric dimensions. At the time that the research was conducted, a dose of 50 mg/day was the standard recommendation for patients. To determine whether this dose was optimal for a given individual, the researchers first exposed participants to low doses, and if no response was noted relative to placebo, then they systematically increased the dose until a response was observed, or until they reached the maximum of 50 mg/day. In general, their method involved a reversal design in which successively higher doses alternated with placebo. So, for example, if one participant did not respond to a low dose, then doses might be increased to generate an ABCD design, where each successive letter represents a higher dose (other sequences were arranged as well). Parametrically examining doses in this way, and examining individual subject data, the researchers found that some participants responded favorably at lower doses than 50 mg/day (e.g., 10 or 20 mg/day). This was an important finding because the higher doses often produced unwanted side effects. Once optimal doses were identified for individuals, the researchers were able to conduct further analyses using a reversal design, exposing them to either their optimal dose or placebo on different days.

Guyatt and colleagues also investigated the minimum duration of treatment necessary to detect an effect [ 5 ]. Initially, all participants were exposed to the medication for 4 weeks. Visual analysis of the time-series data revealed that medication effects were apparent within about 1–2 weeks of exposure, making a 4-week trial unnecessary. This discovery was replicated in a number of subjects and led them to optimize future, larger studies by only conducting a 2-week intervention. Investigating different treatment durations, such as this, is also a parametric analysis.

Parametric analysis can detect effects that may be missed using a standard group design with only one or two values of the independent variable. For example, in the studies conducted by Guyatt and colleagues [ 5 ], if only the lowest dose of amitriptyline had been investigated using a group approach, the researchers may have incorrectly concluded that the intervention was ineffective because this dose only worked for some individuals. Likewise, if only the highest dose had been investigated, it may have been shown to be effective, but potentially more individuals would have experienced unnecessary side effects (i.e., the results would have low social validity for these individuals). Perhaps most importantly, in contrast to what is typically measured in a group design (e.g., means, confidence intervals, etc.), optimizing treatment effects is fundamentally a question about an individual ’ s behavior.

COMPONENT ANALYSIS

A component analysis is “any experiment designed to identify the active elements of a treatment condition, the relative contributions of different variables in a treatment package, and/or the necessary and sufficient components of an intervention” [ 69 ]. Behavioral health interventions often entail more than one potentially active treatment element. Determining the active elements may be important to increase dissemination potential and decrease cost. Single-case research designs, in particular the reversal and multiple-baseline designs, may be used to perform a component analysis. The essential experimental ingredients, regardless of the method, are that the independent variable(s) are systematically introduced and/or withdrawn, combined with replication of effects within and/or between subjects.

There are two main variants of component analyses: the dropout and add-in analyses. In a dropout analysis, the full treatment package is presented following a baseline phase and then components are systematically withdrawn from the package. A limitation of dropout analyses is when components produce irreversible behavior change (i.e., learning a new skill). Given that most interventions seek to produce sustained changes in health-related behavior, dropout analyses may have limited applicability. Instead, in add-in analyses, components can be assessed individually and/or in combination before the full treatment package is assessed [ 69 ]. Thus, a researcher could conduct an ABACAD design, where A is baseline, B and C are the individual components, and D is the combination of the two B and C components. Other sequences are also possible, and which one is selected will require careful consideration. For example, sequence effects should be considered, and researchers could address these effects through counterbalancing, brief “washout” periods, or explicit investigation of these effects [ 26 ]. If sequence effects cannot be avoided, combined SCD and group designs can be used to perform a component analysis. Thus, different components of a treatment package can be delivered between two groups, and within each group, a SCD can be used to assess effects of each combination of components. Although very few component analyses have assessed health behavior or symptoms per se as the outcome measure, there are a variety of behavioral interventions that have been evaluated using component analysis [ 63 ]. For example, Sanders [ 70 ] conducted a component analysis of an intervention to decrease lower back pain (and increase time standing/walking). The analysis consisted of four components: functional analysis of pain behavior (e.g., self-monitoring of pain and the conditions that precede and follow pain), progressive relaxation training, assertion training, and social reinforcement of increased activity. Sanders concluded that both relaxation training and reinforcement of activity were necessary components (see [ 69 ] for a discussion of some limitations of this study).

Several conclusions can be drawn about the effects of the various components in changing behavior. The data should first be evaluated to determine the extent to which the effects of individual components are independent of one another. If they are, then the effects of the components are additive. If they are not, then the effects are multiplicative, or the effects of one component depend on the presence of another component. Figure  3 presents simplified examples of these two possibilities using a reversal design and short data streams (adapted from [ 69 ]). The panel on the left shows additive effects, and the panel on the right shows multiplicative effects. The data also can be analyzed to determine whether each component is necessary and sufficient to produce behavior change. For instance, the panel on the right shows that neither the component labeled X (e.g., self-monitoring of health behavior) nor the component labeled Y (e.g., counseling to change health behavior) is sufficient, and both components are necessary. If two components produce equal changes in behavior, and the same amount of change when both are combined, then either component is sufficient but neither is necessary.

Two examples of possible results from a component analysis. BSL baseline, X first component, Y second component. The panel on the left shows an additive effect of components X and Y, and the panel of the right shows a multiplicative effect of components X and Y

The logic of the component analyses described here is similar to new methods derived from an engineering framework [ 2 , 9 , 71 ]. During the initial stages of intervention development, researchers use factorial designs to allocate participants to different combinations of treatment components. These designs, called fractional factorials because not all combinations of components are tested, can be used to screen promising components of treatment packages. The components tested may be derived from theory or working assumptions about which components and combinations will be of interest, which is the same process used to guide design choices in SCD research. Just as engineering methods seek to isolate and combine active treatment components to optimize interventions, so too do single-case methods. The main difference between approaches is the focus on the individual as the unit of analysis in SCDs.

OPTIMIZING WITH REPLICATIONS AND ESTABLISHING GENERALITY

Another form of optimization is an understanding of the conditions under which an intervention may be successful. These conditions may relate to particular characteristics of the participant (or whatever the unit of analysis happens to be) or to different situations. In other words, optimizing an intervention means establishing its generality.

In the context of single-case research, generality can be demonstrated experimentally in several ways. The most basic way is via direct replication [ 26 ]. Direct replication means conducting the same experiment on the same behavioral problem across several individuals (i.e., a single-case experiment). For example, Raiff and Dallery [ 72 ] achieved a direct replication of the effects of internet-based contingency management (CM) on adherence to glucose testing in four adolescents. One goal of the study was to establish experimental control by the intervention and to minimize as many extraneous factors as possible. Overall, direct replication can help establish generality across participants. It cannot answer questions about generality across settings, behavior change agents, target behaviors, or participants that differ in some way from the original experiment (e.g., to adults diagnosed with type 1 diabetes). Instead, systematic replication can answer these questions. In a systematic replication, the methods from previous direct replication studies are used in a new setting, target behavior, group of participants, and so on [ 73 ]. The Raiff and Dallery study, therefore, was also a systematic replication of effects of internet-based CM to promote smoking cessation to a new problem and to a new group of participants because the procedure had originally been tested with adult smokers [ 24 ]. Effects of internet-based CM for smoking cessation also were systematically replicated in an application to adolescent smokers using a single-case design [ 74 ].

Systematic replication also occurs with parametric manipulation [ 63 ]. In other words, rather than changing the type of participants or setting, we change the value of the independent variable. In addition to demonstrating an optimal effect, parametric analysis may also reveal boundary conditions. These may be conditions under which an intervention no longer has an effect, or points of diminishing returns in which further increases in some parameter produce no further increases in efficacy. For example, if one study was conducted showing that 30 min of moderate exercise produced a decrease in cigarette cravings, a systematic replication, using parametric analysis, might be conducted to determine the effects of other exercise durations (e.g., 5, 30, 60 min) on cigarette craving to identify the boundary parameters (i.e., the minimum and maximum number of minutes of exercise needed to continue to see changes in cigarette craving). Boundary conditions are critical in establishing generality of an intervention. In most cases, the only way to assess boundary conditions is through experimental, parametric analysis of an individual’s behavior.

By carefully choosing the characteristics of the individuals, settings, or other relevant variables in a systematic replication, the researcher can help identify the conditions under which a treatment works. To be sure, as with any new treatment, failures will occur. However, the failure does not detract from the prior successes: “…a procedure can be quite valuable even though it is effective under a narrow range of conditions, as long as we know what those conditions are” [ 75 ]. Such information is important for treatment recommendations in a clinical setting, and scientifically, it means that the conditions themselves may become the subject of experimental analysis.

This discussion leads to a type of generality called scientific generality [ 63 ], which is at the heart of a scientific understanding of behavioral health interventions (or any intervention for that matter). As described by Branch and Pennypacker [ 63 ], scientific generality is characterized by knowledgeable reproducibility, or knowledge of the factors that are required for a phenomenon to occur. Scientific generality can be attained through parametric and component analysis, and through systematic replication. One advantage of a single-case approach to establishing generality is that a series of strategic studies can be conducted with some degree of efficiency. Moreover, the data intimacy afforded by SCDs can help achieve scientific generality about behavioral health interventions.

PERSONALIZED BEHAVIORAL MEDICINE

Personalized behavioral medicine involves three steps: assessing diagnostic, demographic, and other variables that may influence treatment outcomes; assigning an individual to treatment based on this information; and using SCDs to assess and tailor treatment. The first and second steps may be informed by outcomes using SCDs. In addition, the clinician may be in a better position to personalize treatment with knowledge derived from a body of SCD research about generality, boundary conditions, and the factors that are necessary for an effect to occur. (Of course, this information can come from a variety of sources—we are simply highlighting how SCDs may fit in to this process.)

In addition, with advances in genomics and technology-enabled behavioral assessment prior to treatment (i.e., a baseline phase), the clinician may further target treatment to the unique characteristics of the individual [ 76 ]. Genetic testing is becoming more common before prescribing various medications [ 17 ], and it may become useful to predict responses for treatments targeting health behavior. Baseline assessment of behavior using technology such as EMA may allow the clinician to develop a tailored treatment protocol. For example, assessment could reveal the temporal patterning of risky situations, such as drinking alcohol, having an argument, or long periods of inactivity. A text-based support system could be tailored such that the timings of texts are tied to the temporal pattern of the problem behavior. The baseline assessment may also be useful to simply establish whether a problem exists. Also, the data path during baseline may reveal that behavior or symptoms are already improving prior to treatment, which would suggest that other, non-treatment variables are influencing behavior. Perhaps more importantly, compared to self-report, baseline conditions provide a more objective benchmark to assess effects of treatment on behavior and symptoms.

In addition to greater personalization at the start of treatment, ongoing assessment and treatment tailoring can be achieved with SCDs. Hayes [ 77 ] described how parametric and component analyses can be conducted in clinical practice. For example, reversal designs could be used to conduct a component analysis. Two components, or even different treatments, could be systematically introduced alone and together. If the treatments are different, such comparisons would also yield a kind of comparative effectiveness analysis. For example, contingency contracting and pharmacotherapy for smoking cessation could be presented alone using a BCBC design (where B is contracting and C is pharmacotherapy). A combined treatment could also be added, and depending on results, a return to one or the other treatment could follow (e.g., BCDCB, where D is the combined treatment). Furthermore, if a new treatment becomes available, it could be tested relative to an existing standard treatment in the same fashion. One potential limitation of such designs is when a reversal to baseline conditions (i.e., no treatment) is necessary to document treatment effects. Such a return to baseline may be challenging for ethical, reimbursement, and other issues.

Multiple-baseline designs also can be used in clinical contexts. Perhaps the simplest example would be a multiple baseline across individuals with similar problems. Each individual would experience an AB sequence, where the durations of the baseline phases vary. Another possibility is to target different behavior in the same individual in a multiple-baseline across behavior design. For example, a skills training program to improve social behavior could target different aspects of such behavior in a sequential fashion, starting with eye contact, then posture, then speech volume, and so on. If behavior occurs in a variety of distinct settings, the treatment could be sequentially implemented across these settings. Using the same example, treatment could target social behavior at family events, work, and different social settings. It can be problematic if generalization of effects occurs, but it may not necessarily negate the utility of such a design [ 27 ].

Multiple-baseline designs can be used in contexts other than outpatient therapy. Biglan and associates [ 1 ] argued that such designs are particularly useful in community interventions. For example, they described how a multiple baseline across communities and even states could be used to assess effects of changes in drinking age on car crashes. These designs may be especially useful to evaluate technology-based health interventions. A web-based program could be sequentially rolled out to different schools, communities, or other clusters of individuals. Although these research designs are also referred to as interrupted time series and stepped wedge designs, we think it may be more likely for researchers and clinicians to access the rich network of resources, concepts, and analytic tools if these designs are subsumed under the category of multiple-baseline designs.

The systematic comparisons afforded by SCDs can answer several key questions relevant to optimization. The first question a clinician may have is whether a particular intervention will work for his or her client [ 27 ]. It may be that the client has such a unique history and profile of symptoms, the clinician may not be confident about the predictive validity of a particular intervention for his or her client [ 6 ]. SCDs can be used to answer this question. Also, as just described, they can address which of two treatments work better, whether adding two treatments (or components) together works better than either one alone, which level of treatment is optimal (i.e., a parametric analysis), and whether a client prefers one treatment over another (i.e., via social validity assessment). Furthermore, the use of SCDs in practice conforms to the scientist-practitioner ideal espoused by training models in clinical psychology and allied disciplines [ 78 ].

OPTIMIZING FROM DEVELOPMENT TO DISSEMINATION

We are now in a position to evaluate whether SCDs live up to our ideals about optimization. During development, SCDs may obviate some logistical issues in using between-group designs to conduct initial efficacy testing [ 3 , 8 ]. Specifically, the costs and duration needed to conduct a SCD to establish preliminary efficacy would be considerably lower than traditional randomized designs. Riley and colleagues [ 8 ] noted that randomized trials take approximately 5.5 years from the initiation of enrollment to publication, and even longer from the time a grant application is submitted. In addition to establishing whether a treatment works, SCDs have the flexibility to efficiently address which parameters and components are necessary or optimal. In light of traditional methods to establish preliminary efficacy and optimize treatments, Riley and colleagues advocated for “rapid learning research systems.” SCDs are one such system.

Although some logistical issues may be mitigated by using SCDs, they do not necessarily represent easy alternatives to traditional group designs. They require a considerable amount of data per participant (as opposed to a large number of individuals in a group), enough participants to reliably demonstrate experimental effects, and systematic manipulation of variables over a long duration. For the vast majority of research questions, however, SCDs can reduce the resource and time burdens associated with between group designs and allow the investigator to detect important treatment parameters that might otherwise have been missed.

SCDs can minimize or eliminate a number of threats to internal validity. Although a complete discussion of these threats is beyond the scope of this paper (see [ 1 , 27 , 28 ]), the standards listed in Table  1 can provide protection against most threats. For example, the threat known as “testing” refers to the fact that repeated measurement alone may change behavior. To address this, baseline phases need to be sufficiently long, and there must be enough within and/or between participant replications to rule out the effect of testing. Such logic applies to a number of other potential threats (e.g., instrumentation, history, regression to the mean, etc.). In addition, a plethora of new analytic techniques can supplement experimental techniques to make inferences about causal relations. Combining SCD results in meta-analyses can yield information about comparative effects of different treatments, and combing results using Bayesian methods may yield information about likely effects at the population level.

Because of their efficiency and rigor, SCDs permit systematic replications across types of participants, behavior problems, and settings. This research process has also led to “gold-standard,” evidence-based treatments in applied behavior analysis and education [ 29 , 79 ]. More importantly, in several fields, such research has led to scientific understanding of the conditions under which treatment may be effective or ineffective [ 79 , 80 ]. The field of applied behavior analysis, for example, has matured to the extent that individualized assessment of the causes of problem behavior must occur before treatment recommendations.

Our discussion of personalized behavioral medicine highlighted how SCDs can be used in clinical practice to evaluate and optimize interventions. The advent of technology-based assessment makes SCDs much easier to implement. Technology could propel a “super convergence” of SCDs and clinical practice [ 76 ]. Advances in technology-based assessment can also promote the kind of systematic play central to the experimental attitude. It can also allow testing of new interventions as they become available. Such translational efforts can occur in several ways: from laboratory and other controlled settings to clinical practice, from SCD to SCD within clinical practice, and from randomized efficacy trials to clinical practice.

Over the past 70 years, SCD research has evolved to include a broad array of methodological and analytic advances. It also has generated evidence-based practices in health care and related disciplines such as clinical psychology [ 81 ], substance abuse [ 82 , 83 ], education [ 29 ], medicine [ 4 ], neuropsychology [ 30 ], developmental disabilities [ 27 ], and occupational therapy [ 84 ]. Although different methods are required for different purposes, SCDs are ideally suited to optimize interventions, from development to dissemination.

Acknowledgments

We wish to thank Paul Soto for comments on a previous draft of this manuscript. Preparation of this paper was supported in part by Grants P30DA029926 and R01DA023469 from the National Institute on Drug Abuse.

Conflict of interest

The authors have no conflicts of interest to disclose.

Implications

Practitioners: practitioners can use single-case designs in clinical practice to help ensure that an intervention or component of an intervention is working for an individual client or group of clients.

Policy makers: results from a single-case design research can help inform and evaluate policy regarding behavioral health interventions.

Researchers: researchers can use single-case designs to evaluate and optimize behavioral health interventions.

Contributor Information

Jesse Dallery, Phone: +1-352-3920601, Fax: +1-352-392-7985, Email: ude.lfu@yrellad .

Bethany R Raiff, Email: ude.nawor@ffiar .

Single Case Research Design

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This chapter addresses the peculiarities, characteristics, and major fallacies of single case research designs. A single case study research design is a collective term for an in-depth analysis of a small non-random sample. The focus on this design is on in-depth. This characteristic distinguishes the case study research from other research designs that understand the individual case as a rather insignificant and interchangeable aspect of a population or sample. Also, researchers find relevant information on how to write a single case research design paper and learn about typical methodologies used for this research design. The chapter closes with referring to overlapping and adjacent research designs.

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Hunziker, S., Blankenagel, M. (2021). Single Case Research Design. In: Research Design in Business and Management. Springer Gabler, Wiesbaden. https://doi.org/10.1007/978-3-658-34357-6_8

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Evaluating What Works

Chapter 18 single case designs.

The single case design, also known as N-of-1 trial, or small N design, is a commonly used intervention design in speech and language therapy, clinical psychology, education, and neuropsychology, including aphasia therapy ( Perdices & Tate, 2009 ) . The single case design may be regarded as an extreme version of a within-subjects design, where two more more conditions are compared within a single person. This type of trial is sometimes dismissed as providing poor quality evidence, but a well-designed single case trial can be an efficient way to obtain an estimate of treatment efficacy in an individual. Very often, a set of single case trials is combined into a case series (see below). It is important to note that a single case trial is not a simple case report, but rather a study that is designed and analysed in a way that controls as far as possible for the kind of unwanted influences on results described in chapters 2-5.

18.1 Logic of single case designs

Table 18.1 compares the logic of the standard RCT and single case designs.

The first row of Table 18.1 shows the design for a simple 2-arm RCT, where intervention is varied between participants who are assessed on the same occasion and on the same outcome. The second row shows a version of the single case design where the invention is varied in a single subject at different time points. The third row shows the case where intervention is assessed by comparing treated vs untreated outcomes in the same subject on the same occasion - this is referred to by Krasny-Pacini & Evans ( 2018 ) as a multiple baseline design across behaviours and by Ledford et al. ( 2019 ) as an Adapted Alternating Treatment Design.

Whatever design is used, the key requirements are analogous to those of the RCT:

• To minimize unwanted variance (noise) that may mask effects of interest.
• To ensure that the effect we observe is as unbiased as possible.
• To have sufficient data to reliably detect effects of interest

18.1.1 Minimising unwanted variance

In the RCT, this is achieved by having a large enough sample of participants to distinguish variation associated with intervention from idiosyncratic differences between individuals, and by keeping other aspects of the trial, such as timing and outcomes, as constant as possible.

With single case trials, we do not control for variation associated with individual participant characteristics - indeed we are interested in how different people respond to intervention - but we do need to control as far as possible for other sources of variation. The ABA design is a popular single-case design that involves contrasting an outcome during periods of intervention (B) versus periods of no intervention (A). For example, Armson & Stuart ( 1998 ) studied the impact of frequency-altered auditory feedback on 12 people who stuttered. They contrasted a baseline period (A), a period with auditory feedback (B), and a post-intervention period (A), taking several measures of stuttering during each period. Figure 18.1 shows data from two participants during a reading condition. Although the initial amount of stuttering differs for the two individuals, in both cases there is a precipitate drop in stuttering at the 5 minute point corresponding to the onset of the masking, which is sustained for some minutes before gradually rising back towards baseline levels. The baseline period is useful for providing a set of estimates of stuttering prior to intervention, so we can see that the drop in stuttering, at least initially, is outside the range of variation that occurs spontaneously.

Figure 18.1: Outcome over time in a single case ABA design. Redrawn from digitized data from two participants from Figure 2 of Armson et al (1998)

In the context of neurorehabilitation and speech-and-language therapy, there would appear to be a major drawback of the ABA design. In the course of a historical review of this approach, Mirza et al. ( 2017 ) described the “N-of-1 niche” as follows:

“The design is most suited to assessing interventions that act and cease to act quickly. It is particularly useful in clinical contexts in which variability in patient responses is large, when the evidence is limited, and/or when the patient differs in important ways from the people who have participated in conventional randomized controlled trials.”

While the characteristics in the second sentence fit well with speech-and-language therapy interventions, the first requirement - that the intervention should “act and cease to act quickly” is clearly inapplicable. As described in the previous chapter, with few exceptions, interventions offered by those working in education as well as speech and language therapists and those working in other allied health professions are intended to produce long-term change that persists long after the therapy has ended. Indeed, a therapy that worked only during the period of administration would not be regarded as a success. This means that ABA designs, which compare an outcomes for periods with (B) and without (A) intervention, anticipating that scores will go up transiently during the intervention block, will be unsuitable. In this regard, behavioural interventions are quite different from many pharmaceutical interventions, where ABA designs are increasingly being used to compare a series of active and washout periods for a drug.

Despite this limitation, it is feasible to use an approach where we compare different time periods with and without intervention in some situations, most notably when there is good evidence that the targeted behaviour is unlikely to improve spontaneously. Inclusion of a baseline period, where behaviour is repeatedly sampled before intervention has begun, may give confidence that this is the case. An example of this multiple baseline approach from a study by Swain et al. ( 2020 ) is discussed below. Where the same intervention can be applied to a group of participants, then a hybrid method known as the multiple baseline across participants design can be used, which combines both between and within-subjects comparisons. A study of this kind by Koutsoftas et al. ( 2009 ) is discussed in the Class Exercise for this chapter.

In another kind of single case approach, the multiple baseline across behaviours design, it is the outcome measure that is varied. This approach is applicable where a single intervention has potential to target several specific behaviours or skills. This gives fields such as speech and language therapy an edge that drug trials often lack: we can change the specific outcome that is targeted by the intervention and compare it with another outcome that acts as a within-person control measure. To demonstrate effectiveness, we need to show that it is the targeted behaviour that improves, while the comparison behaviour remains unaffected.

For instance, Best et al. ( 2013 ) evaluated a cueing therapy for anomia in acquired aphasia in a case series of 16 patients, with the aim of comparing naming ability for 100 words that had been trained versus 100 untrained words. By using a large number of words, carefully selected to be of similar initial difficulty, they had sufficient data to show whether or not there was selective improvement for the trained words in individual participants.

Figure 18.2 is redrawn from data of Best et al. ( 2013 ) . The black points show N items correct on the two sets of items prior to intervention. They were selected to be of similar difficulty and hence they cluster around the dotted line, which shows the point where scores on both item sets are equivalent. The red points show scores after intervention. Points that fall above the dotted line correspond to cases who did better with trained than untrained words; those below the line did better with untrained than trained words. The red points tend to be placed vertically above the pre-test scores for each individual, indicating that there is improvement after intervention in the trained items (y-axis), but not on control items (x-axis).

Figure 18.2: Outcome over time in multiple outcomes design. Reconstructed data from 16 participants, Best et al (2013)

Given the large number of items in each set, it is possible to do a simple comparison of proportions to see whether each person’s post-intervention score is reliably higher than their pre-intervention score for each item set. For 14 of the 16 cases, there is a statistically significant increase in scores from pre-intervention to post-intervention for target items (corresponding to those with lines that extend vertically above the dotted line), whereas this is the case for only two of the cases when control items are considered (corresponding to cases which show change in the horizontal direction from pre-intervention to post-intervention).

18.1.2 Minimising systematic bias

We have seen in previous chapters how the RCT has evolved to minimize numerous sources of unwanted systematic bias. We need to be alert to similar biases affecting results of single case trials. This is a particular concern for trial designs where we compare different time periods that do or do not include intervention. On the one hand, we may have the kinds of time-linked effects of maturation, practice or spontaneous recovery that lead to a general improvement over time, regardless of the intervention (see Chapter 4 ), and on the other hand there may be specific events that affect a person’s performance, such as life events or illness, which may have a prolonged beneficial or detrimental effect on performance.

The general assumption of this method is that if we use a sufficient number of time intervals, time-linked biases will average out, but while this may be true for transient environmental effects, such as noise or other distractions, it is not the case for systematic influences that continue over time. It is important to be aware of such limitations, and it may be worth considering combining this kind of design with other elements that control for time-related biases more effectively (see below).

18.1.3 The need for sufficient data

Some early single case studies in neuropsychology may have drawn over-optimistic conclusions because they had insufficient replications of outcome measures, assuming that the observed result was a valid indication of outcome without taking into account error of measurement. For instance, if someone’s score improved from 2/10 items correct prior to intervention to 5/10 correct after intervention, it can be hard to draw firm conclusions on the basis of this data alone: the change could just be part of random variability in the measure. The more measurements we have in this type of study, the more confidence we can place in results: whereas in RCTs we need sufficient participants to get a sense of how much variation there is in outcomes, in single case studies we need sufficient observations, and should never rely just a few instances.

In effect, we need to use the same kind of logic that we saw in Chapter 10 , where we estimated statistical power of a study by checking how likely we would be to get a statistically significant result from a given sample size. Table 18.2 shows power to detect a true effect of a given size in a multiple baseline across behaviours design of the kind used by Best et al. ( 2013 ) , where we have a set of trained vs untrained items, each of which is scored either right or wrong. The entries in this table show power, which is the probability that a study would detect a true effect of a given size on a one-tailed test. These entries were obtained by simulating 1000 datasets with each of the different combinations of sample size and effect size.

The columns show the effect size as the raw difference in proportion items correct for trained vs untrained words. It is assumed that these two sets were equated for difficulty prior to intervention, and the table shows the difference in proportion correct between the two sets after intervention. So if the initial proportion correct was .3 for both trained and untrained items, but after intervention, we expect accuracy on trained items to increase to .6 and the untrained to stay at .3, then the difference between the two sets after treatment is .3, shown in the 4th column of the table. We can then read down this column to see the point at which power reaches 80% or more. This occurs at the 4th row of the table, when there are 40 items in each set. If we anticipated a smaller increase in proportion correct for trained items of .2, then we would need 80 items per set to achieve 80% power.

18.2 Examples of studies using different types of single case design

As noted above, single case designs cover a wide range of options, and can vary the periods of observation or the classes of observations made for each individual.

18.2.1 A multiple baseline design: Speech and language therapy for adolescents in youth justice.

The key feature of a multiple baseline design is onset of intervention is staggered across at least three different points in time. Potentially, this could be done by having three or more participants, each of whom was measured in a baseline and an intervention phase, but with the timing of the intervention phase varied across participants. Alternatively, one can have different outcomes assessed in a single participant. Figure 18.3 from Swain et al. ( 2020 ) provides an illustration of the latter approach with a single participant, where different outcomes are targeted at different points in a series of intervention sessions. Typically, the timing of the interventions is not preplanned, but rather, they are introduced in sequence, with the second intervention only started after there is a documented effect from the first intervention, and so on ( Horner & Odom, 2014 ) .

Figure 18.3: Data from one case in the Swain et al. ( 2020 ) study. The shaded region shows sessions with intervention for each of the three outcomes.

The three panels show percentages correct on outcome probes for three skills: spelling-phonics, spelling-morphology and vocabulary. These were targeted sequentially in different sessions, and evidence for intervention effectiveness is obtained when a selective increase in performance is shown for the period during and after intervention. Note that for all three tasks, there is little or no overlap for scores during baseline and those obtained during and after intervention. The baseline data establish that although targeted behaviours vary from day to day, there is no systematic upward trend in performance until the intervention is administered. Furthermore, the fact that improvement is specific to the behaviour that is targeted in that session gives confidence that this is not just down to some general placebo effect.

In the other case studies reported by Swain et al. ( 2020 ) , different behaviours were targeted, according to the specific needs of the adolescents who were studied.

18.2.2 A study using multiple baseline across behaviours: Effectiveness of electropalatography

We noted in the previous chapter how, electropalatography, a biofeedback intervention that provides information about the position of articulators to help clients improve production of speech sounds, is ill-suited to evaluation in a RCT. It is potentially applicable to people with a wide variety of aetiologies, so the treated population is likely to be highly heterogenous, it requires expensive equipment including an individualized artificial palate, and the intervention is delivered over many one-to-one sessions. The goal of the intervention is to develop and consolidate new patterns of articulation that will persist after the intervention ends. It would not, therefore, make much sense to do a single case trial of electropalatography using an ABA design that involved comparing blocks of intervention vs no intervention. One can, however, run a trial that tests whether there is more improvement on targeted speech sounds than on other speech sounds that are not explicitly treated.

Leniston & Ebbels ( 2021 ) applied this approach to seven adolescents with severe speech disorders, all of whom were already familiar with electropalatography. Diagnoses included verbal dyspraxia, structural abnormalities of articulators (velopharyngeal insufficiency), mosaic Turner syndrome, and right-sided hemiplegia. At the start of each school term, two sounds were identified for each case: a target sound, which would be trained, and a control sound, which was also produced incorrectly, but which was not trained. Electropalatography training was administered twice a week in 30 minute sessions. The number of terms where intervention was given ranged from 1 to 3.

Figure 18.4: Individual results for targets and controls at each term (Redrawn Fig 3 from Leniston & Ebbels, data kindly provided by Susan Ebbels)

An analysis of group data found no main effect of target or time, but a large interaction between these, indicating greater improvement on trained speech sounds. The design of the study made it possible to look at individual cases, which gave greater insights into variation of the impact of intervention. As shown in Figure 18.4 , in the first term of intervention, there was a main effect of time for three of the participants (IDs 1, 3, and 4), but no interaction with sound type. In other words, these children improved over the course of the term, but this was seen for the untrained as well as the trained sound. By term 2, one of four children showed an interaction between time and sound type (ID4), and both children who continued training into term 3 (ID 1 and 2) showed such an interaction. Three children did not show any convincing evidence of benefit - all of these stopped intervention after one term.

As the authors noted, there is a key limitation of the study: when a significant interaction is found between time and sound type, this provides evidence that the intervention was effective. But when both trained and untrained sounds improve, this is ambiguous. It could mean that the intervention was effective, and its impact generalized beyond the trained sounds. But it could also mean that the intervention was ineffective, with improvement being due to other factors, such as maturation or practice on the outcome measure. Inclusion of a series of baseline measures might have helped establish how plausible these two possibilities were.

In sum, this method can handle the (typical) situation where intervention effects are sustained, but it is most effective if we do not expect any generalization of learning beyond the targeted behaviour or skill. Unfortunately, this is often at odds with speech and language therapy methods. For instance, in phonological therapy, the therapist may focus on helping a child distinguish and/or produce a specific sound pair, such as [d] vs [g], but there are good theoretical reasons to expect that if therapy is successful, it might generalize to other sound pairs, such as [t] vs [k], which depend on the same articulatory contrast between alveolar vs velar place. Indeed, if we think of the child’s phonology as part of a general system of contrasts, it might be expected that training on one sound pair could lead the whole system to reorganize. This is exactly what we would like to see in intervention, but it can make single case studies extremely difficult to interpret. Before designing such a study, it is worthwhile anticipating different outcomes and considering how they might be interpreted.

18.2.3 Example of an analysis of case series data

The terms ‘single case’ and ‘N-of-1’ are misleading in implying that only one participant is trained. More commonly, studies assemble a series of N-of-1 cases. Where the same intervention is used for all cases, regular group statistics may be applied. But unlike in RCTs, heterogeneity of response is expected and needs to be documented. In fact, in a single case case series, the interest is less in whether an overall intervention effect is statistically significant, as in whether the data provide evidence of individual variation in response to intervention, as this is what would justify analysis of individual cases. Formally, it is possible to test whether treatment effects vary significantly across participants by comparing a model that does or does not contain a term representing this effect, using linear mixed models , but we would recommend that researchers consult a statistician, as those methods are complex and require specific types of data. In practice, it is usually possible to judge how heterogeneous responses to intervention are by inspecting plots for individual participants.

Typically the small sample sizes in N-of-1 case series preclude any strong conclusions about the characteristics of those who do and do not show intervention effects, but results may subsequently be combined across groups, and specific hypotheses formulated about the characteristics of those who show a positive response.

An example comes from the study by Best et al. ( 2013 ) evaluating rehabilitation for anomia in acquired aphasia. As described above, researchers contrasted naming ability for words that had been trained, using a cueing approach, versus a set of untrained control words, a multiple baseline across behaviours design. In general, results were consistent with prior work in showing that improvement was largely confined to trained words. As noted above, this result allows us to draw a clear conclusion that the intervention was responsible for the improvement, but from a therapeutic perspective it was disappointing, as one might hope to see generalization to novel words.

The authors subdivided the participants according to their language profiles, and suggested that improvement on untrained words was seen in a subset of cases with a specific profile of semantic and phonological strengths. This result, however, was not striking and would need to be replicated.

18.2.4 Combining approaches to strengthen study design

In practice, aspects of different single-case designs can be combined - e.g. the cross-over design by Varley et al. ( 2016 ) that we described in Chapter 17 compared an intervention across two time points and two groups of participants, and also compared naming performance on three sets of items: trained words, untrained words that were phonemically similar to the trained words, and untrained words that were dissimilar to the trained words. Furthermore, baseline measures were taken in both groups to check the stability of naming responses. That study was not, however, analysed as a single case design: rather the focus was on average outcomes without analysing individual differences. However, the inclusion of multiple outcomes and multiple time points meant that responses of individuals could also have been investigated.

18.3 Statistical approaches to single case designs

Early reports of single case studies often focused on simple visualization of results to determine intervention effects, and this is still a common practice ( Perdices & Tate, 2009 ) . This is perfectly acceptable provided that differences are very obvious, as in Figure 18.1 above. We can think back to our discussion of analysis methods for RCTs: the aim is always to ask whether the variation associated with differences in intervention is greater than the variation within the intervention condition. In Figure 18.1 there is very little overlap in the values for the intervention vs non-intervention periods, and statistics are unnecessary. However, results can be less clearcut than this. Figure 18.5 shows data from two other participants in the study by Armson & Stuart ( 1998 ) , where people may disagree about whether or not there was an intervention effect. Indeed, one criticism of the use of visual analysis in single case designs is that it is too subjective, with poor inter-rater agreement about whether effects are seen. In addition, time series data will show dependencies: autocorrelation. This can create a spurious impression of visual separation in data for different time periods ( Kratochwill et al., 2014 ) . A more quantitative approach that adopts similar logic is to measure the degree of non-overlap between distributions for datapoints associated with intervention and those from baseline or control conditions ( Parker et al., 2014 ) . This has the advantage of simplicity, and relative ease of interpretation, but may be bedevilled by temporal trends in the data, and have relatively low statistical power unless there are large numbers of observations.

Figure 18.5: Outcome over time in a single case ABA design. Digitized data from two participants from Figure 2 of Armson et al (1998)

Unfortunately, rather than a well-worked-out set of recommendations for statistical analysis of single case trials, there is a plethora of methods in use, which can be challenging, or even overwhelming, for anyone starting out in this field to navigate ( Kratochwill & Levin, 2014 ) . Furthermore, most of the focus has been on ABA and related designs, with limited advice on how to deal with designs that use comparisons between treated and untreated outcomes.

Our view is that single-case designs have considerable potential. There has been much argument about how one should analyse single case study data; multilevel models have been proposed as a useful way of answering a number of questions with a single analysis - how large the treatment effect is for individual cases, how far the effect varies across cases, and how large the average effect is. However, caution has been urged, because, as Rindskopf & Ferron ( 2014 ) noted, these more complex models make far more assumptions about the data than simpler models, and results may be misleading if they are not met. We suggest that the best way to find the optimal analysis method may be to simulate data from a single-case study design, so that one can then compare the power and efficiency of different analytic approaches, and also their robustness to aspects of the data such as departures from normality. Simulation of such data is complicated by the fact that repeated observations from a single person will show autocorrelation, but this property can be incorporated in a simulation. A start has been made on this approach: see this website by James Pustejovsky. The fact that single-case studies typically make raw data available means there is a wealth of examples that could be tested in simulations.

18.4 Overview of considerations for single case designs

In most of the examples used here, the single case design could be embedded in natural therapy sessions, include heterogeneous participants, and be adapted to fit into regular clinical practice. This makes the method attractive to clinicians, but it should be noted that while incorporating evaluation into clinical activities is highly desirable, it often creates difficulties for controlling aspects of internal validity. For instance, in the study by Swain et al. ( 2020 ) , the researchers noted an element of unpredictability about data collection, because the young offenders that they worked with might either be unavailable, or unwilling to take part in intervention sessions on a given day. In the Leniston & Ebbels ( 2021 ) study the target and control probes were not always well-matched at baseline, and for some children, the amount of available data was too small to give a powerful test of the intervention effect. Our view is that it is far better to aim to evaluate interventions than not to do so, provided limitations of particular designs are understood and discussed. Table 18.3 can be used as a checklist against which to assess characteristics of a given study, to evaluate how far internal validity has been controlled.

We are not aware of specific evidence on this point, but it seems likely that the field of single case studies, just like other fields, is likely to suffer from problems of publication bias (Chapter 19 ), whereby results are reported when an intervention is successful, but not when it fails. If studies are adequately powered - and they should be designed so that they are - then all results should be reported, including those which may be ambiguous or unwanted, so that we can learn from what doesn’t work, as well as from what does.

A final point, which cannot be stressed enough, is that when evaluating a given intervention, a single study is never enough. Practical constraints usually make it impossible to devise the perfect study that gives entirely unambiguous results: rather we should aim for our studies to reduce the uncertainty in our understanding of the effectiveness of intervention, with each study building on those that have gone before. With single case studies, it is common to report the raw data in the paper, in either numeric or graphical form, and this is particularly useful in allowing other researchers to combine results across studies to form stronger conclusions (see Chapter 21 ).

18.5 Class exercise

• Koutsoftas et al. ( 2009 ) conducted a study of effectiveness of phonemic awareness intervention with a group of children who showed poor sound awareness after receiving high quality whole-classroom teaching focused on this skill. Intervention sessions were administered by speech-language pathologists or experienced teachers to 13 groups of 2-4 children twice per week for a baseline and post-intervention period, and once per week during the 6 week intervention. Active intervention was preceded by a baseline period - one week (with two outcome measurement points) for seven groups of children, and two weeks (4 measurement points) for the other six groups. Outcome probes involved identifying the initial sound from a set of three words in each session. The researchers reported effect sizes for individual children that were calculated by comparing score on the probes in the post-intervention period with those in the baseline period, showing that most children showed significant gains on the outcome measure. Group results on the outcome measure (redrawn from Table 2 of the paper) are shown in Figure 18.6 .

Figure 18.6: Group means from Koutsoftas et al, 2009. Filled points show intervention phase, unfilled show baseline or post-intervention

Consider the following questions about this study. a. What kind of design is this? b. How well does this design guard against the biases shown in Table 18.3 ? c. Could the fact that intervention was delivered in small groups affect study validity? (Clue: see Chapter 16 ). d. If you were designing a study to follow up on this result, what changes might you make to the study design? e. What would be the logistic challenges in implementing these changes?

The SCRIBE guidelines have been developed to improve reporting of single case studies in the literature. An article by Tate et al. ( 2016 ) describing the guidelines with explanation and elaboration is available here , with a shorter article summarising the guidelines here . Identify a single case study in the published literature in your area and check it against the guidelines to see how much of the necessary information is provided. This kind of exercise can be more useful than just reading the guidelines, as it forces the reader to read an article carefully and consider what the guidelines mean.

In the previous chapter, we described a study by Calder et al. ( 2021 ) , which used a cross-over design to evaluate the effect of an intervention designed to improve grammatical morphology. This study also included probes to test mastery of untrained morphological endings. The trained structure was past tense -ed; a ‘generalization’ probe was another verb ending, 3rd person singular -s, and a control probe was possessive -s. Before studying Figure 18.7 make a note of your predictions about what you might expect to see with these additional probes.

Figure 18.7: Mean % correct for all 3 probes in delayed cross-over study by Calder et al, 2021 (data plotted from Calder et al’s Table 2).

Once you have studied the Figure, consider whether you think the inclusion of the probes has strengthened your confidence in the conclusion that the intervention is effective.

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Article Contents

Initial steps, premeeting activities, consensus meeting, postmeeting activities, postpublication activities, conclusions, the single-case reporting guideline in behavioural interventions (scribe) 2016 statement.

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Robyn L. Tate, Michael Perdices, Ulrike Rosenkoetter, William Shadish, Sunita Vohra, David H. Barlow, Robert Horner, Alan Kazdin, Thomas Kratochwill, Skye McDonald, Margaret Sampson, Larissa Shamseer, Leanne Togher, Richard Albin, Catherine Backman, Jacinta Douglas, Jonathan J. Evans, David Gast, Rumen Manolov, Geoffrey Mitchell, Lyndsey Nickels, Jane Nikles, Tamara Ownsworth, Miranda Rose, Christopher H. Schmid, Barbara Wilson, The Single-Case Reporting Guideline In BEhavioural Interventions (SCRIBE) 2016 Statement, Physical Therapy , Volume 96, Issue 7, 1 July 2016, Pages e1–e10, https://doi.org/10.2522/ptj.2016.96.7.e1

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We developed a reporting guideline to provide authors with guidance about what should be reported when writing a paper for publication in a scientific journal using a particular type of research design: the single-case experimental design. This report describes the methods used to develop the Single-Case Reporting guideline In BEhavioural interventions (SCRIBE) 2016. As a result of 2 online surveys and a 2-day meeting of experts, the SCRIBE 2016 checklist was developed, which is a set of 26 items that authors need to address when writing about single-case research. This article complements the more detailed SCRIBE 2016 Explanation and Elaboration article ( Tate et al., 2016 ) that provides a rationale for each of the items and examples of adequate reporting from the literature. Both these resources will assist authors to prepare reports of single-case research with clarity, completeness, accuracy, and transparency. They will also provide journal reviewers and editors with a practical checklist against which such reports may be critically evaluated. We recommend that the SCRIBE 2016 is used by authors preparing manuscripts describing single-case research for publication, as well as journal reviewers and editors who are evaluating such manuscripts.

Reporting guidelines, such as the Consolidated Standards of Reporting Trials (CONSORT) Statement, improve the reporting of research in the medical literature ( Turner et al., 2012 ). Many such guidelines exist and the CONSORT Extension to Nonpharmacological Trials ( Boutron et al., 2008 ) provides suitable guidance for reporting between-groups intervention studies in the behavioral sciences. The CONSORT Extension for N -of-1 Trials (CENT 2015) was developed for multiple crossover trials with single individuals in the medical sciences ( Shamseer et al., 2015 ; Vohra et al., 2015 ), but there is no reporting guideline in the CONSORT tradition for single-case research used in the behavioral sciences. We developed the Single-Case Reporting guideline In BEhavioural interventions (SCRIBE) 2016 to meet this need. This Statement article describes the methodology of the development of the SCRIBE 2016, along with the outcome of 2 Delphi surveys and a consensus meeting of experts. We present the resulting 26-item SCRIBE 2016 checklist. The article complements the more detailed SCRIBE 2016 Explanation and Elaboration article ( Tate et al., 2016 ) that provides a rationale for each of the items and examples of adequate reporting from the literature. Both these resources will assist authors to prepare reports of single-case research with clarity, completeness, accuracy, and transparency. They will also provide journal reviewers and editors with a practical checklist against which such reports may be critically evaluated.

Keywords: single-case design, methodology, reporting guidelines, publication standards

Supplemental materials: http://dx.doi.org/10.1037/arc0000026.supp

University courses generally prepare students of the behavioral sciences very well for research using parallel, between-groups designs. By contrast, single-case methodology is “rarely taught in undergraduate, graduate and postdoctoral training” ( Kazdin, 2011 , p. vii). Consequently, there is a risk that researchers conducting and publishing studies using single-case experimental designs (and journal reviewers of such studies) are not necessarily knowledgeable about single-case methodology nor well trained in using such designs in applied settings. This circumstance, in turn, impacts the conduct and report of single-case research. Even though single-case experimental intervention research has comparable frequency to between-groups research in the aphasiology, education, psychology, and neurorehabilitation literature ( Beeson & Robey, 2006 ; Perdices & Tate, 2009 ; Shadish & Sullivan, 2011 ), evidence of inadequate and incomplete reporting is documented in multiple surveys of this literature in different populations ( Barker et al., 2013 ; Didden et al., 2006 ; Maggin et al., 2011 ; Smith, 2012 ; Tate et al., 2014 ).

To address these issues we developed a reporting guideline, entitled the Single-Case Reporting guideline In BEhavioural interventions (SCRIBE) 2016, to assist authors, journal reviewers and editors to improve the reporting of single-case research. This Statement provides the methodology and development of the SCRIBE 2016. The companion SCRIBE 2016 Explanation and Elaboration (E&E) article ( Tate et al., 2016 ) provides detailed background to and rationale for each of the 26 items in the SCRIBE checklist, along with examples of adequate reporting in the published literature.

The SCRIBE 2016 Statement is intended for use with the family of single-case experimental designs 1 used in the behavioral sciences. It applies to four prototypical designs (withdrawal/reversal, multiple-baseline, alternating-treatments, and changing-criterion designs), including combinations and variants of these designs, as well as adaptive designs. Figure 1 presents the common designs using a single case based on surveys in the literature (see, e.g., Perdices & Tate, 2009 ; Shadish & Sullivan, 2011 ).

Common designs in the literature using a single participant. Reproduced from the expanded manual for the Risk of Bias in N -of-1 Trials (RoBiNT) Scale ( Tate et al., 2015 ) with permission of the authors; an earlier version of the figure, taken from the original RoBiNT Scale manual ( Tate et al., 2013a ) was also published in 2013 ( Tate et al., 2013b ).

The figure mainly draws on the behavioral sciences literature, which includes a broad range of designs using a single participant. Only those designs above the solid horizontal line use single-case methodology (i.e., an intervention is systematically manipulated across multiple phases during each of which the dependent variable is measured repeatedly and, ideally, frequently). None of the designs below the solid horizontal line meets these criteria and they are not considered single-case experiments: The B-phase training study comprises only a single (intervention) phase; the so-called “pre–post” study does not take repeated measurements during the intervention phase; and the case description is a report, usually compiled retrospectively, that is purely descriptive without systematic manipulation of an intervention.

The A-B design, also labeled “phase change without reversal” ( Shadish & Sullivan, 2011 ), is widely regarded as the basic single-case design. It differs from the “pre–post” study in that measurement of the dependent variable occurs during the intervention (B) phase. In the Figure , we place the A-B design in an intermediate position between the nonexperimental single-case designs (below the solid horizontal line) and the four experimental designs above the dotted horizontal line because it has weak internal validity, there being no control for history or maturation, among other variables. As a result, it is regarded as a quasiexperimental design ( Barlow et al., 2009 ).

Designs above the dotted horizontal line are experimental in that the control of threats to internal validity is stronger than in the A-B design. Nonetheless, within each class of design the adequacy of such controls and whether or not the degree of experimental control meets design standards (see Horner et al., 2005 ; Kratochwill et al., 2013 ) vary considerably (cf. A-B-A vs. A-B-A-B; multiple-baseline designs with two vs. three baselines/tiers). Consequently, reports of these designs in the literature have variable scientific quality and features of internal and external validity can be evaluated with scales measuring scientific robustness in single-case designs, such as described in Maggin et al. (2014) and Tate et al. (2013b) .

The structure of the four prototypical experimental designs in Figure 1 differ significantly: The withdrawal/reversal design systematically applies and withdraws an intervention in a sequential manner, the multiple-baseline design systematically applies an intervention in a sequential manner that also has a staggered introduction across a particular parameter (e.g., participants, behaviors), the alternating/simultaneous-treatments design compares multiple interventions in a concurrent manner by rapidly alternating the application of the interventions, and the changing-criterion design establishes a number of hierarchically based criterion levels that are implemented in a sequential manner. Each of the single-case experimental designs has the capacity to introduce randomization into the design (cf. the small gray rectangle within each of the designs in Figure 1 ), although in practice randomization in single-case research is not common.

The medical N -of-1 trial is depicted within the withdrawal/reversal paradigm of Figure 1 . The analogous reporting guide for the medical sciences, CONSORT Extension for N -of-1 Trials (CENT 2015; Shamseer et al., 2015 ; Vohra et al., 2015 ), is available for the reporting of medical N -of-1 trials. These trials consist of multiple cross-overs (described as challenge-withdrawal-challenge-withdrawal in Vohra et al.) in a single participant who serves as his or her own control, often incorporating randomization and blinding.

As with other reporting guidelines in the CONSORT tradition, the SCRIBE 2016 does not make recommendations about how to design, conduct or analyze data from single-case experiments. Rather, its primary purpose is to provide authors with a checklist of items that a consensus from experts identified as the minimum standard for facilitating comprehensive and transparent reporting. This checklist includes the specific aspects of the methodology to be reported and suggestions about how to report. Consequently, readers are provided with a clear, complete, accurate, and transparent account of the context, plan, implementation and outcomes of a study. Readers will then be in a position to critically evaluate the adequacy of the study, as well as to replicate and validate the research. Clinicians and researchers who want guidance on how to design, conduct and analyze data for single-case experiments should consult any of the many current textbooks and reports (e.g., Barker et al., 2011 ; Barlow, Nock, & Hersen, 2009 ; Gast & Ledford, 2014 ; Horner et al., 2005 ; Kazdin, 2011 ; Kennedy, 2005 ; Kratochwill et al., 2013 ; Kratochwill & Levin, 2014 ; Morgan & Morgan, 2009 ; Riley-Tilman & Burns, 2009 ; Vannest, Davis, & Parker, 2013 ), as well as recent special issues of journals (e.g., Journal of Behavioral Education in 2012, Remedial and Special Education in 2013, the Journal of School Psychology and Neuropsychological Rehabilitation in 2014, Aphasiology in 2015) and methodological quality recommendations ( Horner et al., 2005 ; Kratochwill et al., 2013 ; Maggin et al., 2014 ; Smith, 2012 ; Tate et al., 2013b ).

The impetus to develop the SCRIBE 2016 arose during the course of discussion at the CENT consensus meeting in May 2009 in Alberta, Canada (see Shamseer et al., 2015 ; Vohra et al., 2015 ). The CENT initiative was devoted to developing a reporting guideline for a specific design and a specific discipline: N -of-1 trials in the medical sciences. At that meeting the need was identified for development of a separate reporting guideline for the broader family of single-case experimental designs as used in the behavioral sciences (see Figure 1 ).

A 13-member steering committee for the SCRIBE project was formed comprising a Sydney, Australia, executive (authors RLT, convenor, and SM, MP, LT, with UR appointed as project manager). An additional three members who had spearheaded the CENT initiative (CENT convenor, SV, along with MS and LS) were invited because of their experience and expertise in developing a CONSORT-type reporting guideline in a closely related field ( N -of-1 trials). In order to ensure representation from experts in areas of single-case investigations in clinical psychology, special education and single-case methodology and data analysis, another five experts were invited to the steering committee (authors DHB, RH, AK, TK, and WS). Of course, other content experts exist who would have been eligible for the steering committee, but a guiding consideration was to keep the number of members to a reasonable size so that the project was manageable. In the early stages of the project, steering committee members were instrumental in item development and refinement for the Delphi survey.

The methodology used to develop the SCRIBE 2016 followed the procedures outlined by Moher et al. (2010) . At the time of project commencement, the literature on evidence of bias in reporting single-case research was very limited and it has only recently started to emerge. Members of the steering committee, however, were already knowledgeable about the quality of the existing single-case literature, which had prompted independent work in the United States (specifically in compiling competency standards of design and evidence; Hitchcock et al., 2014 ; Horner et al., 2005 ; Kratochwill et al., 2010 , 2013 ) and Australia (in developing an instrument to evaluate the scientific quality of single-case experiments; Tate et al., 2008 , 2013b ). No reporting guideline, in the CONSORT tradition, emerged from literature review.

Since commencement of the SCRIBE project, a reporting guide for single-case experimental designs was published by Wolery, Dunlap, and Ledford (2011) . That guide was not developed following the same series of steps as in previously developed reporting guidelines such as those of the CONSORT family (see Moher et al., 2011 ) and is not as comprehensive as the CONSORT-type guidelines on which the current project is based, covering about half of the items in the SCRIBE 2016. Nevertheless, the convergence between the recommendations of Wolery and colleagues regarding the need to report on features such as inclusion and exclusion criteria for participants, design rationale, operational definitions of the target behavior versus the corresponding items presented in the SCRIBE 2016 is noteworthy and adds validity to the SCRIBE 2016. Funding for the SCRIBE project was obtained from the Lifetime Care and Support Authority of New South Wales, Australia. The funds were used to employ the project manager, set up and develop a web-based survey, hold a consensus meeting, and sponsor participants to attend the consensus meeting.

Methodology of the Delphi Process

The Delphi technique is a group decision-making tool and consensus procedure that is well suited to establishing expert consensus on a given set of items ( Brewer, 2007 ). The nature of the process allows for it to be conducted online, and responses can be given anonymously. The Delphi procedure consists of several steps, beginning with the identification, selection, and invitation of a panel of experts in the pertinent field to participate in the consensus process. Subsequently, the items are distributed to experts who rate the importance of each topic contained in the items. As we did for the present project, a Likert scale is often used, ranging from 1 to 10, whereby 1 indicates very low importance and 10 very high importance . All expert feedback is then collated and reported back to the panel, including the mean, standard deviation, and median for each item, a graph indicating the distribution of responses, as well as any comments made by other experts to inform further decision-making. When high consensus is achieved, which may take several rounds, the Delphi exercise is completed. Von der Gracht (2012) reviews a number of methods to determine consensus for the Delphi procedure. Methods include using the interquartile range (IQR), with consensus operationalized as no more than 2 units on a 10-unit scale.

The SCRIBE Delphi Procedure

A set of potential items was drawn up by the SCRIBE steering committee for the Delphi survey. The items initially came from two sources available at the time: (a) those identified in a systematic review previously conducted by the CENT group ( Punja et al., in press ), and subsequently refined during the CENT consensus meeting process, and (b) items used to develop the Single-Case Experimental Design Scale published by the Sydney-based members as part of an independent project ( Tate et al., 2008 ). Steering committee members suggested additional items, as well as rephrasing of existing items. We formatted the resulting 44 initial items for distribution in the Delphi exercise, using an online survey tool, SurveyMonkey.

Two rounds of a Delphi survey were conducted in April and September 2011. Figure 2 provides a flow diagram of the Delphi survey participants. In total, we identified 131 experts worldwide as potential Delphi panel members (128 for the initial round and an additional three participants were added at Round 2) based on their track record of published work in the field of single-case research (either methodologically or empirically based) and/or reporting guideline development. We used several strategies to identify suitable respondents. The Sydney executive drew up lists of authors who published single-case experimental designs in the behavioral sciences, by consulting reference lists of books and journal articles and our PsycBITE database ( www.psycbite.com ). We examined the quality of authors' work, as described in their reports, using our methodological quality scale ( Tate et al., 2008 ), and invited authors of scientifically sound reports. In addition, we conducted Google searches of editorial board members of journals that were known to publish single-case reports, as well as the authors publishing in such journals and evaluated the quality of their work. Finally, steering committee members made recommendations of suitable authors. This group of 131 invitees represents a sample of all world experts. We distributed invitations by e-mail for ease of communication and speed of contact. An “opt-in” consent arrangement was used and thus consent to participate required the invitee's active response. Of the pool of 128 invitations for Round 1, 54 did not respond to the invitation (we sent one reminder e-mail), eight did respond but declined (mainly on the grounds of not having sufficient time), and four e-mail addresses were undeliverable. The remaining 62 responders who consented to participate in Round 1 were sent the survey link.

Flow diagram of the Delphi surveys.

In Round 1, 53 of 62 consenting experts responded within the 2-week time frame of the survey, with 50 providing a complete data set of responses to the original set of 44 items. Results were entered into a database. Importance ratings of the items were uniformly high, with no item receiving a group median rating <7/10. The items thus remained unrevised for Round 2, which was conducted to elicit additional comment on the items. These decision-making criteria are compatible with that used in the development of the CENT 2015, which excluded items with mean importance ratings <5/10 ( Vohra et al., 2015 ).

For Round 2, the survey link was sent to 59 of the original 62 consenting participants to Round 1 (the three participants who consented but did not complete Round 1 did not provide reasons for their early discontinuance and were not recontacted), and an additional three experts recommended by steering committee members. Graphed results were provided to respondents, along with anonymous comments on the items from the other panel members. A complete data set of responses for Round 2 was collected from 45 participants. Again, the ratings of importance for each item were mostly very high, all items having median importance ratings of at least 8/10, but the range of responses decreased. According to the criteria of von der Gracht (2012) consensus was achieved for 82% of items (36/44) which had IQRs of 2 or less on the 10-point scale. The remaining eight items had IQRs from 2.25 to 4 and were discussed in detail at the consensus meeting.

As depicted in Figure 2 , across the two rounds of the Delphi exercise 65/131 invited experts consented to participate (62 participants in Round 1 and an additional three participants in Round 2). Forty participants provided a complete data set of responses to both Round 1 and Round 2, representing a 62% response rate (40/65). The 40 responders represented 31% of the total of 131 experts invited to participate in the survey.

Sixteen world experts in single-case methodology and reporting guideline development attended a 2-day consensus meeting, along with the Sydney executive and two research staff. Representation included clinical-research content experts in clinical and neuropsychology, educational psychology and special education, medicine, occupational therapy, and speech pathology; as well as single-case methodologists and statisticians; journal editors and a medical librarian; and guideline developers. Delegates met in Sydney on December 8 and 9, 2011. Each participant received a folder which contained reference material pertinent to the SCRIBE project, and results from both rounds of the Delphi survey. Each of the Delphi items contained a graph of the distribution of scores, the mean and median scores of each round of the survey, along with the delegate's own scores when s/he completed the Delphi surveys.

The meeting commenced with a series of brief presentations from steering committee members on the topics of reporting guideline development, single-case methods and terminology, evolution of the SCRIBE project, and description of the CENT. Results of the Delphi survey were then presented. Delegates had their folder of materials to consult and a PowerPoint presentation that projected onto a screen to facilitate discussion. A primary aim of the consensus meeting was to develop the final set of items for the SCRIBE checklist. The final stages of the meeting discussed the documents to be published, authorship, and knowledge dissemination strategy.

During the meeting the 44 Delphi items were discussed, item by item, over the course of four sessions, each led by two facilitators. The guiding principles for discussion were twofold. First, item content was scrutinized to ensure that (a) it captured the essence of the intended issue under consideration and (b) the scope of the item covered the necessary and sufficient information to be reported. Second, the relevance of the item was examined in terms of its capacity to ensure clarity and accuracy of reporting.

Three delegates at the consensus meeting (authors RLT and SM, and a research staff member, DW) took notes about the amalgamation and merging of items where applicable and refinements to wording of items. Final wording of items was typed, live-time, into a computer that projected onto a screen so that delegates could see the changes, engage in further discussion, give approval, and commit to the group decision. In addition, the meeting was audiotaped for the purpose of later transcription to have a record of the discussion of the items and inform the direction and points to describe in the E&E document.

Figure 3 illustrates the discussion process that occurred during the consensus meeting. The figure presents a screen-shot of the PowerPoint presentation of one of the items (Item 31 of the Delphi survey, Treatment Fidelity, which was broadened to encompass procedural fidelity as a result of discussion at the consensus meeting, and became item 17 of the SCRIBE). The figure shows the results of each round of the Delphi survey (the results for Round 1 and Round 2 appear in the Figure as the left- and right-sided graphs respectively), along with discussion points. These points comprised comments made by the Delphi survey participants when completing the online surveys, as well as suggestions prepared by the Sydney executive that emerged from the consolidated comments. The points were used to stimulate discussion among the conference delegates, but discussion was not restricted to the prepared points.

Screen-shot of a discussion item at the consensus meeting.

By the end of the meeting, delegates reached consensus on endorsing 26 items that thus constitute the minimum set of reporting items comprising the SCRIBE 2016 checklist. The SCRIBE 2016 checklist consists of six sections in which the 26 aspects of report writing pertinent to single-case methodology are addressed. The first two sections focus on the title/abstract and introduction, each section containing two items. Section 3, method, consists of 14 items addressing various aspects of study methodology and procedure. Items include description of the design (e.g., randomization, blinding, planned replication), participants, setting, ethics approval, measures and materials (including the types of measures, their frequency of measurement, and demonstration of their reliability), interventions, and proposed analyses. The results (Section 4) and discussion (Section 5), each contains three items. Section 6 (documentation) contains two items pertaining to protocol availability and funding for the investigation.

In total, 24 Delphi were merged into seven SCRIBE items because they referred to the same topics: (a) SCRIBE Item 5 (design) contained three Delphi items (design structure, number of sequences, and decision rules for phase change); (b) Item 8 (randomization), two Delphi items (sequence and onset of randomization); (c) Item 11 (participant characteristics), two Delphi items (demographics and etiology); (d) Item 13 (approvals), two Delphi items (ethics approval and participant consent); (e) Item 14 (measures), nine Delphi items (operational definitions of the target behavior, who selected it, how it was measured, independent assessor blind to phase, interrater agreement, follow-up measures, measures of generalization and social validity, and methods to enhance quality of measurement); (f) Item 19 (results), two Delphi items (sequence completed and early stopping); and (g) Item 20 (raw data), four Delphi items (results, raw data record, access to raw data, and stability of baseline). One of the Delphi items relating to meta-analysis, was considered not to represent a minimum standard of reporting for single-case experimental designs and accordingly was deleted.

The audio recording of the 2-day consensus meeting was transcribed. The final guideline items were confirmed after close examination of the conference transcript and the SCRIBE 2016 checklist was developed (see Table 1 ). The meeting report was prepared and distributed to the steering committee members in June 2012. The Sydney executive then began the process of drafting background information sections for each item and integrating these with the broader literature for the E&E article. Multiple versions of the E&E article were distributed over the next 2 years to the steering committee members for their comment and subsequent versions incorporated the feedback.

The Single-Case Reporting Guideline In BEhavioural Interventions (SCRIBE) 2016 Checklist

Authors can use the checklist to help with writing a research report and readers (including journal editors/reviewers) can use the checklist to evaluate whether the report meets the points outlined in the guideline. Users will find the detailed SCRIBE 2016 E&E document ( Tate et al., 2016 ) helpful for providing rationale for the items, with examples of adequate reporting from the literature.

Following publication of this SCRIBE 2016 Statement and the E&E article ( Tate et al., 2016 ), the next stage of activity focuses on further dissemination. Obtaining journal endorsement for the SCRIBE 2016 is a vital task because it has been demonstrated that journals that endorse specific reporting guidelines are associated with better reporting than journals where such endorsement does not exist ( Turner et al., 2012 ). The SCRIBE project is indexed on the EQUATOR network ( http://www.equator-network.org/ ) and a SCRIBE website ( www.sydney.edu.au/medicine/research/scribe ) provides information and links to the SCRIBE 2016 publications. SCRIBE users are encouraged to access the website and provide feedback on their experiences using the SCRIBE and suggestions for future revisions of the guideline. Future research will evaluate the uptake and impact of the SCRIBE 2016.

We expect that the publication rate of single-case experiments and the research into single-case methodology will expand over the years, given the evidence of such a trend (e.g., Hammond & Gast, 2010 ) and also considering the recent interest shown in journal publication of special issues dedicated to single-case design research referred to earlier in this article. As is common for guidelines, the SCRIBE 2016 will likely require updates and revisions to remain current and aligned with the best evidence available on methodological standards.

We developed the SCRIBE 2016 to provide authors, journal reviewers, and editors with a recommended minimum set of items that should be addressed in reports describing single-case research. Adherence to the SCRIBE 2016 should improve the clarity, completeness, transparency, and accuracy of reporting single-case research in the behavioral sciences. In turn, this will facilitate (a) replication, which is of critical importance for establishing generality, (b) the coding of different aspects of the studies as potential moderators in meta-analysis, and (c) evaluation of the scientific quality of the research. All of these factors are relevant to the development of evidence-based practices.

Single-case methodology is defined as the intensive and prospective study of the individual in which (a) the intervention/s is manipulated in an experimentally controlled manner across a series of discrete phases, and (b) measurement of the behavior targeted by the intervention is made repeatedly (and, ideally, frequently) throughout all phases. Professional guidelines call for the experimental effect to be demonstrated on at least three occasions by systematically manipulating the independent variable ( Horner et al., 2005 ; Kratochwill et al., 2010 , 2013 ). This criterion helps control for the confounding effect of extraneous variables that may adversely affect internal validity (e.g., history, maturation) and allows a functional cause and effect relationship to be established between the independent and dependent variables.

The SCRIBE Group wishes to pay special tribute to our esteemed colleague Professor William Shadish (1949–2016) who passed away on the eve of publication of this article. His contribution at all stages of the SCRIBE project was seminal.

Funding for the SCRIBE project was provided by the Lifetime Care and Support Authority of New South Wales, Australia. The funding body was not involved in the conduct, interpretation or writing of this work. We acknowledge the contribution of the responders to the Delphi surveys, as well as administrative assistance provided by Kali Godbee and Donna Wakim at the SCRIBE consensus meeting. Lyndsey Nickels was funded by an Australian Research Council Future Fellowship (FT120100102) and Australian Research Council Centre of Excellence in Cognition and Its Disorders (CE110001021). For further discussion on this topic, please visit the Archives of Scientific Psychology online public forum at http://arcblog.apa.org .

In order to encourage dissemination of the SCRIBE Statement, this article is freely accessible through Archives of Scientific Psychology and will also be published in the American Journal of Occupational Therapy , Aphasiology , Canadian Journal of Occupational Therapy , Evidence-Based Communication Assessment and Intervention , Journal of Clinical Epidemiology , Journal of School Psychology , Neuropsychological Rehabilitation , Physical Therapy , and Remedial and Special Education . The authors jointly hold the copyright for this article.

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This paper is in the following e-collection/theme issue:

Published on 1.4.2024 in Vol 11 (2024)

A Novel Blended Transdiagnostic Intervention (eOrygen) for Youth Psychosis and Borderline Personality Disorder: Uncontrolled Single-Group Pilot Study

Authors of this article:

Original Paper

• Shaunagh O'Sullivan 1, 2 , BA, MPsychSc   ; 
• Carla McEnery 1, 2 , BPsychSc (Hons), PhD   ; 
• Daniela Cagliarini 1, 2 , BA, GDipPsych, PG Dip Psych, MPsych   ; 
• Jordan D X Hinton 1, 2, 3 , BA, GDip(Psych)   ; 
• Lee Valentine 1, 2 , BA, MSocWk, PhD   ; 
• Jennifer Nicholas 1, 2 , BA, BSc (Hons), PhD   ; 
• Nicola A Chen 1, 2 , BSc (Hons), PhD   ; 
• Emily Castagnini 1, 2 , BSci, MPH   ; 
• Jacqueline Lester 1 , MPsych   ; 
• Esta Kanellopoulos 1 , BA/LLB, MPsych/PhD   ; 
• Simon D'Alfonso 4 , BASc (Hons), PhD   ; 
• John F Gleeson 3 , BA (Hons), MPsych, PhD   ; 
• Mario Alvarez-Jimenez 1, 2 , DClinPsy, MAResearchMeth, PhD  

1 Orygen, Parkville, Australia

2 Centre for Youth Mental Health, University of Melbourne, Melbourne, Australia

3 Health Brain and Mind Research Centre, School of Behavioural and Health Sciences, Australian Catholic University, Melbourne, Australia

4 School of Computing and Information Systems, University of Melbourne, Melbourne, Australia

Corresponding Author:

Shaunagh O'Sullivan, BA, MPsychSc

35 Poplar Road

Phone: 61 428282470

Email: [email protected]

Background: Integrating innovative digital mental health interventions within specialist services is a promising strategy to address the shortcomings of both face-to-face and web-based mental health services. However, despite young people’s preferences and calls for integration of these services, current mental health services rarely offer blended models of care.

Objective: This pilot study tested an integrated digital and face-to-face transdiagnostic intervention (eOrygen) as a blended model of care for youth psychosis and borderline personality disorder. The primary aim was to evaluate the feasibility, acceptability, and safety of eOrygen. The secondary aim was to assess pre-post changes in key clinical and psychosocial outcomes. An exploratory aim was to explore the barriers and facilitators identified by young people and clinicians in implementing a blended model of care into practice.

Methods: A total of 33 young people (aged 15-25 years) and 18 clinicians were recruited over 4 months from two youth mental health services in Melbourne, Victoria, Australia: (1) the Early Psychosis Prevention and Intervention Centre, an early intervention service for first-episode psychosis; and (2) the Helping Young People Early Clinic, an early intervention service for borderline personality disorder. The feasibility, acceptability, and safety of eOrygen were evaluated via an uncontrolled single-group study. Repeated measures 2-tailed t tests assessed changes in clinical and psychosocial outcomes between before and after the intervention (3 months). Eight semistructured qualitative interviews were conducted with the young people, and 3 focus groups, attended by 15 (83%) of the 18 clinicians, were conducted after the intervention.

Results: eOrygen was found to be feasible, acceptable, and safe. Feasibility was established owing to a low refusal rate of 25% (15/59) and by exceeding our goal of young people recruited to the study per clinician. Acceptability was established because 93% (22/24) of the young people reported that they would recommend eOrygen to others, and safety was established because no adverse events or unlawful entries were recorded and there were no worsening of clinical and social outcome measures. Interviews with the young people identified facilitators to engagement such as peer support and personalized therapy content, as well as barriers such as low motivation, social anxiety, and privacy concerns. The clinician focus groups identified evidence-based content as an implementation facilitator, whereas a lack of familiarity with the platform was identified as a barrier owing to clinicians’ competing priorities, such as concerns related to risk and handling acute presentations, as well as the challenge of being understaffed.

Conclusions: eOrygen as a blended transdiagnostic intervention has the potential to increase therapeutic continuity, engagement, alliance, and intensity. Future research will need to establish the effectiveness of blended models of care for young people with complex mental health conditions and determine how to optimize the implementation of such models into specialized services.

Introduction

The evolution of specialist early intervention services for youth represents a major global reform of mental health services [ 1 - 3 ]. However, there are shortcomings that remain to be addressed for these services to fully deliver on their promise; for example, 42% of young people drop out of treatment by the third therapy session [ 4 ], indicating low engagement rates with early intervention services [ 5 ]. Furthermore, those who continue treatment receive time-limited support [ 6 ], and up to 80% of young people with severe mental health conditions will incur repeated relapses, leading to long-term disability and high societal cost [ 7 , 8 ]. Estimates suggest that the cost associated with recurring mental ill-health is up to 5 times that of nonrelapsing presentations [ 9 ]. Even when young people receive evidence-based treatment, its effectiveness is limited [ 10 ]; for example, between one-third and two-thirds of young people do not experience symptom reduction [ 11 ], and functional impairment often remains an issue after remission [ 12 ].

Digital technologies have the potential to address these challenges and limitations by enhancing the accessibility, impact, reach, and cost-effectiveness of youth mental health (YMH) services [ 13 , 14 ]. Many young people, recognizing their need for help, are turning to technology, including smartphone apps, websites, and social media, to self-manage their mental well-being [ 15 ]. Research findings support the efficacy of digital mental health interventions in improving treatment outcomes in severe mental health conditions such as psychosis [ 16 - 18 ] and borderline personality disorder (BPD) [ 19 ]. Web-based treatment programs have also demonstrated efficacy comparable to that of face-to-face psychotherapy [ 20 - 22 ], and self-guided smartphone-based mental health interventions are proving to be promising self-management tools for depression and anxiety symptoms [ 23 ].

However, despite the evidence for the effectiveness of digital interventions, limitations have also been reported, such as high attrition rates [ 24 , 25 ], a focus on mild to moderate mental health conditions [ 26 - 28 ], a focus on single disorders ignoring potential comorbidity [ 29 ], and a lack of integration within clinical settings [ 30 , 31 ]. Factors affecting attrition and dropout from digital interventions have been identified, such as a lack of personalization within digital interventions and severe mental disorders hampering engagement with interventions [ 32 ]. Most of the first generation of digital interventions have also been deployed and evaluated without face-to-face care, generating a divide between face-to-face and digital supports [ 33 ]. Furthermore, clinical trials of digital interventions often recruit highly motivated early adopters from the community, resulting in poor generalizability of the findings in clinical settings [ 33 , 34 ].

Blended care refers to treatment that includes face-to-face and digital elements, both of which contribute to the treatment process and can be integrated or offered sequentially [ 35 , 36 ]. Blended models of care offer an innovative approach to address the limitations of both face-to-face and digital therapy for young people with serious mental illness, while maintaining the strengths of both modalities [ 36 , 37 ]. This integrated approach is in line with World Health Organization recommendations [ 38 ] and young people’s preferences, as well as national and international calls for the integration of web-based and in-person mental health services [ 39 ]. Young people have indicated that blended models of care could enhance clinical care by increasing accessibility and continuity of care, providing access to posttherapy support, and strengthening the relationship with their clinician [ 40 ]. However, despite young people’s preferences and calls for the integration of face-to-face and web-based services [ 16 , 41 ], current mental health services rarely provide this type of integrated web-based support [ 42 ]. Barriers to implementing digital interventions in clinical settings have also been identified, such as a lack of time for clinicians and skepticism toward digital interventions [ 43 ], and these need to be taken into account when developing blended interventions. Furthermore, there is limited research testing blended models of care as a treatment approach [ 37 , 44 ], despite the demonstrated efficacy of stand-alone digital interventions [ 45 - 47 ].

Furthermore, transdiagnostic interventions that target underlying mechanisms or symptoms that are common across multiple mental disorders have the potential to provide more effective, personalized, and engaging treatment, addressing comorbidity and being applicable to a wider range of young people [ 48 , 49 ]. Evidence also suggests that transdiagnostic interventions may be at least as effective, more engaging, and easier to scale up in real-world clinical settings compared with single-disorder interventions [ 50 , 51 ].

As blended transdiagnostic interventions for first-episode psychosis and BPD have not yet been evaluated, a 3-month pilot evaluation of a blended transdiagnostic digital intervention (eOrygen) designed to enhance the accessibility, responsiveness, and impact of face-to-face specialized YMH clinical services for youth psychosis and BPD was carried out. Pilot studies are an important first step before running a full-powered clinical trial because they focus on whether an intervention can be carried out, whether it would be worth proceeding with it, and how to proceed before focusing on evaluating the effectiveness of the intervention [ 52 ].

The primary objective of the eOrygen pilot was to evaluate the feasibility, acceptability, and safety of an integrated web-based clinic that blends moderated online social therapy (MOST) support with face-to-face specialized YMH clinical services for youth psychosis and BPD. A secondary aim of the pilot was to assess changes in key clinical and psychosocial outcomes for young people from the point of enrollment in eOrygen to after the intervention. Furthermore, the failure to integrate digital technologies into routine practice is well documented [ 53 ], and, therefore, an additional objective of this study was to understand young people’s and clinicians’ experiences of barriers and facilitators to using a blended model of care in clinical practice.

Study Design

This was a 3-month multisite pre-post single-group pilot study conducted at the Early Psychosis Prevention and Intervention Centre (EPPIC) and the Helping Young People Early (HYPE) Clinic at Orygen Youth Health in Melbourne, Victoria, Australia. EPPIC provides services for young people aged 15 to 25 years experiencing their first episode of psychosis, and admission to the service is based on a clinical assessment determining the presence of full-threshold first-episode psychosis, including full-threshold psychotic symptoms such as hallucinations, delusions, or formal thought disorder [ 54 ]. The HYPE Clinic offers an early intervention program for young people aged 15 to 25 years with BPD, and intake to the service is based on meeting ≥3 BPD criteria according to the DSM-5 ( Diagnostic and Statistical Manual of Mental Disorders [Fifth Edition]) Text Revision [ 55 ]. These services deliver specialized early interventions, with treatment offered from 6 months to a maximum of 2 years. Each young person at Orygen Youth Health receives case management by a dedicated mental health clinician, with additional assessment and treatment support provided by a psychiatrist. Each year, approximately 155 young people access HYPE Clinic services, and approximately 250 young people access EPPIC services.

Sample Size

It is recommended that the sample size of a pilot study be approximately 10% of the sample size projected for the larger parent study [ 56 ]. At present, there is little definitive research available to determine the sample size of the larger parent randomized controlled trial for a transdiagnostic blended model of care, hence the importance of conducting this pilot feasibility study. In a recent study using the same technology, a total sample of 140 participants was determined to detect changes in social functioning at 90% power, accounting for attrition of 20% [ 57 ]. Given this, we proposed to recruit 25 clinicians and 1 to 2 young people per clinician, resulting in an anticipated 25 to 50 young people in the study.

Ethics Approval

Ethics approval was obtained from the Melbourne Health Human Research Ethics Committee (HREC/49492/MH-2019).

Participants and Procedure

The participants were 18 mental health clinicians and 33 young people recruited by participating clinicians and the Orygen research team across HYPE Clinic and EPPIC clinical services. Clinician recruitment took place over a 2-month period, and the recruitment of young people took place over a 4-month period from May 15 to September 25, 2020.

Young People

Inclusion and exclusion criteria.

Young people were recruited via their clinician and the research team. Clinicians within each service were invited to identify potentially eligible young people based on the following criteria: (1) aged 15 to 25 years (inclusive), (2) currently receiving treatment at the HYPE Clinic or EPPIC, (3) engaged with treatment as judged by the treating clinician and not approaching discharge from service, (4) willing to nominate an emergency contact person, (5) have regular and ongoing internet and telephone access, and (6) able to give informed consent and comply with study procedures. The exclusion criteria were as follows: (1) young people with an intellectual disability who were unable to meet the cognitive demands of the web-based intervention, interfering with the likelihood of benefiting from the intervention as judged by their treating clinician; and (2) young people with an inability to converse in, or read, English. There were no specific exclusion criteria related to level of suicide risk or interpersonal hostility (ie, a consideration for harm to self or others while engaging within a web-based social network). However, clinicians were consulted on a case-by-case basis regarding participant suitability, and clinician judgment regarding suitability could be reassessed at any time. The exclusion criteria for the pilot study were kept to a minimum both to facilitate the recruitment process and to ensure that the intervention was tested and adequately mirrored the real-world characteristics of the broad population of young people accessing specialist YMH services. Furthermore, to mirror the intended real-world implementation of eOrygen, these exclusion criteria were assessed and monitored by the participating clinicians.

Recruitment Process

Once eligibility was determined, eligible young people were invited to participate in the study by the research team. Among the HYPE Clinic clients, of the 106 young people who were assessed for eligibility for this study, 42 (39.6%) met the inclusion criteria; however, 23 (55%) of these 42 young people could not be approached because of their involvement with another research study. Thus, 19 young people were approached to participate, and 15 (79%) agreed to participate and enrolled in the study, whereas 4 (21%) declined. Of the 106 young people assessed for eligibility, 64 (60.4%) were ineligible to participate in this study owing to clinical risk, poor engagement with treatment, a lack of access to technology, age, or because they were approaching discharge.

Among the EPPIC clients, of the 59 young people who were assessed for eligibility, 43 (73%) met the inclusion criteria; however, 3 (7%) of these 43 young people were already participating in another research study. Thus, 40 young people were approached to participate, and 20 (50%) agreed to participate, whereas 11 (28%) declined, and 9 (23%) could not be contacted by the research team. Of the 20 young people who agreed to participate, 2 (10%) could not be contacted to complete their baseline assessments and did not enroll in the study; the remaining 18 (90%) enrolled in the study. However, of these 18 young people, 7 (39%) were lost to follow-up during the study period (n=3, 43% before onboarding to the eOrygen platform and n=4, 57% before completing the 3-month follow-up assessments). The young people lost to follow-up were unresponsive to telephone calls and messages from the research team but were still engaged with face-to-face treatment with their clinicians. Of the 59 young people assessed for eligibility, 16 (27%) were ineligible to participate in this study for the same aforementioned reasons.

Participant consent was obtained from those interested in participating and parental or guardian consent was also obtained for young people aged <18 years.

Assessments

The consenting young people were contacted at baseline via email and telephone to complete baseline measures before setting up their eOrygen user account. The young people then continued treatment with their clinician while having access to the eOrygen platform for 3 months. They were contacted again at the end of the 3-month intervention to complete the postintervention assessments.

During postintervention follow-up telephone call assessments, the young people were asked whether they were willing to be contacted for a subsequent qualitative interview, and 19 (58%) of the 33 young people agreed to be followed up. After the intervention phase, a randomly selected subgroup comprising 12 (63%) of the 19 young people who agreed to be contacted were invited via SMS text messaging to participate. These semistructured qualitative interviews were designed to explore their experiences with the eOrygen platform. The primary goal of these interviews was to identify both barriers and facilitators to their engagement with the intervention.

Of the 12 young people approached after the intervention, 1 (8%) declined to participate (no reason provided), and 2 (17%) agreed to participate but did not attend the scheduled interviews and were not able to be contacted; thus, 9 (75%) participants successfully completed the interview process. However, a technical issue resulted in a recording failure during 1 (11%) of the 9 interviews, and it could not be included in the subsequent analysis.

The interviews were all conducted via Zoom (Zoom Video Communications, Inc), and interview times ranged from 22 to 38 minutes. Participants were recruited and interviewed by a study research assistant and author EC. Interview questions were underpinned by a user-centered design approach [ 24 ] and focused on the following aspects: what initially interested participants about using the eOrygen platform; the experience of onboarding; hopes and expectations; barriers and facilitators; and the overall experience of the therapy journeys, clinical and peer support, and community features of the platform.

All mental health clinicians employed at the HYPE Clinic and EPPIC were eligible for inclusion in this study. Clinicians attended a workshop focused on learning about the background of the intervention, including previous empirical findings using the same technology and how to use the eOrygen platform. The latter aspect concerned how to use the intervention functions and set up an account, with suggestions provided on how to integrate this into the clinicians’ work with young people, with the possibility of using it within and between face-to-face sessions as they felt appropriate. This included clinical case studies that applied to the populations of both HYPE Clinic and EPPIC services and were coauthored by clinicians at these services. Clinicians were also provided a training manual that was used to help them navigate the platform during the workshop and also to keep and reuse as necessary when navigating the intervention platform independently. As the workshop was held before recruiting young people to the study, clinicians were provided with a training video at a later date describing once again how to use the intervention platform features.

Eligible clinicians were then invited to identify eligible young people who met the aforementioned inclusion criteria. All participating clinicians had at least 1 young person using the eOrygen platform. The clinicians were contacted via email at baseline to complete the clinician-rated measures. They were then invited to use the eOrygen platform with their clients for 3 months. At the end of the intervention, they were contacted again via email to complete the postintervention clinician-rated measures.

After the postintervention phase, an invitation was extended to all 18 clinicians to participate in a structured focus group session. The aim of this session was to delve into the obstructive and conducive factors influencing the effective implementation of the eOrygen platform into routine clinical practice. This evaluative process was grounded in the Consolidated Framework for Implementation Research (CFIR), a recognized and widely used framework for assessing the determinants influencing implementation in health care settings [ 58 ]. The interview schedule was designed by author LV and based on the CFIR constructs that were identified via both formal and informal consultation with the specialist service settings throughout the intervention period. Among the notable constructs under consideration were those related to evidence, adaptability, complexity, needs and resources, and self-efficacy.

Clinicians were invited via email and supported by their line managers to attend. Of the 18 clinicians, 15 (83%) were available to participate in the focus groups that were conducted over Zoom. Because of the number of clinicians available to participate, the focus groups were divided into 3 distinct sessions to facilitate more extensive discussions and allow individual clinicians ample opportunity to share their insights and experiences. Authors LV, DC, and EK each conducted 1 of the 3 parallel sessions.

Intervention: eOrygen

The eOrygen intervention was based on Orygen Digital’s MOST model, which was the first digital solution to offer continuous integrated face-to-face and digital care to young people across the mental health diagnostic and severity spectrum and stages of treatment [ 59 - 61 ]. In partnership with young people, the MOST model was iteratively developed by a multidisciplinary team of researchers, clinical psychologists, programmers, creative writers, graphic artists, and experts in human-computer interaction [ 61 - 63 ]. A recent clinical trial with young people with psychosis demonstrated that an intervention based on the MOST model was effective in improving vocational and educational outcomes as well as reducing the use of emergency services; in addition, it was cost-effective, with evidence of a dose-response effect [ 60 , 64 , 65 ].

The eOrygen intervention was a purpose-built web-based platform designed to integrate face-to-face and web-based support for young people experiencing mental ill-health ( Figure 1 ). This was achieved through the use of both clinician and young person user accounts, making it possible for young people and their treating clinician to use the platform throughout the treatment process, during their face-to-face sessions or between sessions. Young people could also use the platform in a self-directed way, but no automated prompts or reminders were provided for young people to use eOrygen between sessions, unless clinicians made suggestions to their young clients using the platform.

The platform was designed to enhance, not replace, recommended treatments for mental health conditions (eg, clinician-administered cognitive behavioral therapy). eOrygen comprised interactive user-directed psychosocial interventions ( therapy journeys ), a social network, clinical moderation, and peer support.

Therapy journeys comprised collections of therapy activities relating to different themes. Themes related to the treatment of mental ill-health, such as managing social anxiety, anxiety, and depression, as well as social functioning. Users were assigned a suggested therapy journey based on their responses to a questionnaire they completed after being onboarded to the eOrygen platform, providing personalized content specific to their individual mental health concerns ( Figure 2 ). Users could complete multiple therapy journeys , and clinicians or young people could change the assigned journey.

Therapy activities could be accessed as part of a therapy journey or as stand-alone activities via the explore function. The explore function enabled young people to use a search bar to locate therapy content of interest, and eOrygen clinicians could also recommend personalized content to young people using this function. Therapy activities included activities , comics , talking points , and actions . Activities comprised written content, and comics comprised storyboard panels focusing on a particular therapeutic theme and target related to the treatment of mental ill-health challenges. Talking points enabled participants to propose a solution to identified problems (eg, how to incorporate mindfulness into everyday activities), which encouraged social problem-solving and effective peer modeling. Actions were behavioral prompts that young people could complete to translate learning on a mental health topic into behavior change.

The eOrygen social network was moderated by trained peer workers, who were young people who had a lived experience of mental illness. The social network included a community newsfeed and individual profile pages where participants and peer workers could create posts to share thoughts, information, pictures, and videos ( Figure 3 ). They could also respond to other users’ posts through comments or reactions . Reactions were designed to facilitate social support (eg, “I get you” and “Thinking of you”). Likewise, talking points were designed as collaborative spaces to discuss specific topics by leaving comments . Young people were also able to receive direct support from peer workers and clinicians on the platform via private messages .

Outcome Measures

Feasibility.

The feasibility of eOrygen was measured by tracking recruitment to the study, which is in line with other studies testing the feasibility of digital interventions [ 66 ]. Although no a priori minimum or maximum number of participants per clinician or per clinic was specified, to accurately assess feasibility, we anticipated recruiting approximately 15 clinicians from EPPIC and 1 to 2 young people per each participating clinician as well as 10 clinicians from the HYPE Clinic and 1 to 2 young people per clinician.

Feasibility was indicated if (1) the recruitment goal was met and (2) the participant refusal rate was <50%. If the recruitment goal was not met after 2 months of recruitment, barriers to recruitment were to be identified.

Acceptability

Intervention acceptability was measured via responses to a feedback questionnaire. The pilot was considered to indicate acceptability of the eOrygen intervention if at least 90% of the young people reported that they would recommend it to others, which is in line with a previous pilot study testing the acceptability of a digital mental health intervention [ 59 ].

Intervention safety was measured by analyzing reports of any adverse events, tracking the security of the web-based system, and analyzing responses to a feedback questionnaire, following a similar protocol for a previous study [ 7 , 67 ]. An adverse event was defined as any unfavorable or unintended sign, symptom, or disease temporally associated with the use of the intervention, whether or not it was related to the intervention. A serious adverse event was defined as any untoward medical occurrence that could be life threatening, result in death, require inpatient hospitalization, or result in persistent or significant disability. All participants were closely monitored by clinical moderators for adverse events and serious adverse events. The research team members were trained in study procedures, including adverse event assessments, and attended good clinical practice training. In addition, treating clinicians were asked to report any adverse events, including suicide attempts and serious self-harm, to the research team.

The pilot was considered to indicate the safety of eOrygen if (1) there were no unlawful entries recorded in the eOrygen system during the pilot, (2) no young people experienced a serious adverse event as a result of their engagement with the system during the 3-month intervention period, (3) at least 95% of the young people reported it to be safe via the feedback questionnaire, and (4) clinical and social measures did not show a worsening pattern over the course of the study.

Safety was also reported by assessing pre-post changes in BPD symptomatology for HYPE Clinic participants as measured by the 23-item version of the Borderline Symptom List [ 68 ], and pre-post changes in psychotic symptoms for EPPIC participants as measured by 3 items of the expanded Brief Psychiatric Rating Scale (version 4.0), including suspiciousness, hallucinations, and unusual thought content [ 69 ].

Potential Clinical Effects

Potential clinical effects were assessed by measuring pre- to postintervention changes in clinical and psychosocial outcomes at baseline and at 3 months. Clinician-rated measures included social and occupational functioning as measured by the Social and Occupational Functioning Assessment Scale [ 70 ] and therapeutic alliance (TA) as measured by the Working Alliance Inventory–Short Revised (therapist version) [ 71 ].

Young people self-report measures included depression as measured by the Patient Health Questionnaire-9 [ 72 ]; TA with their face-to-face clinician as measured by the Working Alliance Inventory–Short Revised (client version) [ 73 ]; psychological well-being as measured by the Flourishing Scale [ 74 ]; self-determination as measured by the Basic Psychological Needs Satisfaction Questionnaire [ 75 ]; loneliness as measured by the University of California, Los Angeles Loneliness Scale (version 3) [ 76 ]; social isolation as measured by the Friendship Scale [ 77 ]; social anxiety as measured by the Social Interaction Anxiety Scale [ 78 ]; stress as measured by the Perceived Stress Scale [ 79 ]; and psychological distress as measured by the 10-item Kessler Psychological Distress Scale [ 80 ]. These measures have been validated in a youth population and were chosen for their demonstrated reliability. All baseline measures were completed before onboarding participants to the eOrygen platform, and all assessments were completed via Qualtrics (Qualtrics International Inc) where possible or otherwise administered by a research assistant over the telephone.

Satisfaction Survey Feedback

Purpose-designed questionnaires administered via Qualtrics were used to assess user satisfaction and user feedback.

Statistical Analyses

This study used a mixed methods design involving both quantitative and qualitative data, which allowed for a more robust analysis [ 81 ]. Quantitative data assessing the feasibility, acceptability, safety, and potential clinical effects of the intervention were measured at baseline and at 3-month follow-up. Qualitative data were used to assess young people’s and clinicians’ barriers and facilitators to implementing eOrygen within clinical services, which enhanced our understanding of the feasibility and acceptability aspects of the intervention and provided valuable information for designing a full-powered trial that would have not been achieved through quantitative data strands alone.

Quantitative Analyses

Chi-square tests showed no differences between the clinical sites in baseline demographic and clinical and psychosocial outcomes. Therefore, data were pooled, repeated measures 2-tailed t tests were conducted, and within-group effect sizes (Cohen d ) were reported for changes in pre- to postintervention scores on effectiveness outcome measures. Parametric and nonparametric correlations were conducted to explore the association between the use of eOrygen and the degree of change between before and after the intervention on effectiveness outcome measures, but no relationships between use and effectiveness outcomes were found.

Aggregated data from the user satisfaction questionnaire and descriptive statistics from insights into using eOrygen were reported as exploratory findings. The data for the acceptability criterion of whether young people would recommend eOrygen to others were derived from insights into eOrygen descriptive statistics. The data for 1 of the safety criteria regarding whether young people felt safe using eOrygen were derived from the user satisfaction questionnaire. Statistical analyses were performed using SPSS (version 27.0; IBM Corp).

Qualitative Analyses

Given the user-centered design approach, thematic analysis was considered the most appropriate method of data analysis [ 82 ]. The data analysis was conducted by author EC under the supervision of author LV.

The analysis process used an inductive approach in which EC explored young people’s experiences for factors relating to barriers and facilitators to young people’s engagement with the blended model of care. To gain familiarity with the data set, the interview transcripts were read and reread. Subsequently, initial codes were applied to the transcripts to identify relevant factors to engagement. Any recurring codes, both within and across different transcripts, were identified and recorded.

Following the principles of thematic analysis, these codes were then grouped into preliminary themes and subjected to thorough review in relation to all other identified themes. Some themes were identified as superordinate, representing broader categories of experience, whereas others assumed subordinate positions, delineating into subthemes.

Three focus groups were conducted by authors DC, EK, and LV with 15 service clinicians overall. Focus groups comprised a mix of both HYPE Clinic and EPPIC clinicians and lasted between 31 and 44 minutes. Interview questions were underpinned by the CFIR [ 58 ], which is one of the most widely used frameworks for identifying factors impacting implementation outcomes [ 83 ]. The CFIR comprises 39 constructs across 5 domains. The domains identified as most relevant to this implementation setting in the preimplementation phase were inner and outer settings , individual characteristics , and innovation characteristics . The clinician focus groups underwent deductive coding by authors JN and LV in accordance with the CFIR. JN and LV then engaged in a rigorous discussion to examine how the attributes within the identified domains acted as either obstacles or enablers to the implementation of eOrygen in this clinical setting.

Use Metrics

Use metrics were used to measure engagement with eOrygen. Number of active days was used as an overall metric for platform use and referred to the number of days a young person accessed eOrygen after completing onboarding until the end of the 3-month intervention period.

Therapy views comprised the number of times a young person opened therapy activities via a therapy journey or via a search function. Users were encouraged to revisit activities, and repeat views were counted within the number of therapy views . Journey components completed was a count of the number of unique therapy activities a user completed within a therapy journey .

Engagement with the social networking component of eOrygen was measured by the number of posts , comments , and reactions made by young people on the social network. This included posts made on the newsfeed and on individual users’ profiles. Comments made could be in response to posts made by other users or peer workers or talking point therapy activities. Reactions made could be in response to any post or comment on the social network.

There was also a chat function where young people could communicate with eOrygen staff (clinicians and peer workers) through private direct messages on the platform. Engagement with clinicians and peer workers was measured by the number of messages sent (by young people) and the number of messages received (from clinicians or peer workers).

Demographics

Participants were aged between 15 and 24 (mean 19.48, SD 2.84) years, and the majority were female individuals (21/33, 64%). Of the 33 participants, 27 (82%) were born in Australia, 7 (21%) spoke languages other than English at home, 3 (9%) identified as Aboriginal or Torres Strait Islander, 9 (27%) were engaged in paid work, and 22 (66%) were studying part time or full time ( Table 1 ).

a HYPE: Helping Young People Early.

b EPPIC: Early Psychosis Prevention and Intervention Centre.

We sought to recruit 25 clinicians; the final number of clinicians enrolled in the study was 18 (78%). The final number of young people recruited was 33 (which exceeded our goal of 1 young person per clinician). We also anticipated that the refusal rate would be <50%, which it was at 25% (15/59).

We exceeded our acceptability goal, with 92% (22/24) of the young people reporting that they would recommend eOrygen to others ( Multimedia Appendix 1 ).

There were no unlawful entries recorded on the eOrygen platform during the study, there were no serious adverse events experienced by participants, there was no worsening of clinical and social outcome measures, and 96% (24/25) of the young people stated that they felt safe using the platform ( Multimedia Appendix 2 ).

In terms of symptom monitoring, the mean score for BPD symptomatology for HYPE Clinic participants reduced from 2.65 (SD 0.75) at baseline to 1.99 (SD 0.83) after the intervention. For the assessment of psychotic symptoms in EPPIC participants, the mean score for suspiciousness reduced from 2.72 (SD 1.64) at baseline to 0.94 (SD 3.78) after the intervention. In addition, the mean score for hallucinations reduced from 2.89 (SD 1.97) at baseline to 1.22 (SD 4.11) after the intervention, and the mean score for unusual thought content reduced from 1.72 (SD 1.13) at baseline to 0.67 (SD 3.74) after the intervention.

Significant pre- to postintervention improvements were observed for 9 (82%) of the 11 clinical outcome measures, including social and occupational functioning, depression, psychological distress, social anxiety, social isolation, stress, borderline symptoms, and loneliness, as well as all aspects of therapist-rated working alliance, including goal, task, and bond, with effect sizes ranging from 0.56 to 0.89 ( Table 2 ).

a BPNS: Basic Psychological Needs Satisfaction.

b PHQ-9: Patient Health Questionnaire (9-item version).

c SIAS: Social Interaction Anxiety Scale.

d PSS: Perceived Stress Scale.

e K10: Kessler Psychological Distress Scale (10-item version).

f WAI-SRC: Working Alliance Inventory–Short Revised (client version).

g WAI-SRT: Working Alliance Inventory–Short Revised (therapist version).

h SOFAS: Social and Occupational Functioning Assessment Scale (clinician rated).

Young People’s Satisfaction Survey Feedback

In terms of client feedback, 88% (21/24) of the young people reported that they would use eOrygen again. The top initial reasons of interest in using eOrygen included (1) practicing well-being skills (22/24, 92%), (2) contributing to research (22/24, 92%), (3) receiving support from clinicians (17/24, 71%), (4) connecting with others with similar mental health experiences (17/24, 71%), and (5) learning and well-being (17/24, 71%). Multimedia Appendix 1 presents a full list of reasons for the young people’s use of eOrygen.

In terms of the young people’s satisfaction with eOrygen, 96% (23/24) rated it as a positive experience, 88% (22/25) rated it as easy to use, and 83% (20/25) rated it as helpful ( Multimedia Appendix 2 ).

A total of 30 young people were onboarded to eOrygen (n=15, 50% from the HYPE Clinic and n=15, 50% from EPPIC). The mean number of active days on eOrygen was 8.4 (SD 7.5) days; 50% (15/30) of the young people had between 6 and 30 active days , 43% (13/30) had between 2 and 5 active days , and 7% (2/30) had 1 active day ( Table 3 ). Of the 30 young people, 12 (40%) used the platform at least once per fortnight during the initial 6 weeks of the intervention, and 6 (20%) maintained fortnightly access across the entire 12 weeks.

In terms of therapy engagement specifically, 40% (12/30) of the young people viewed ≥3 therapy activities, 23% (7/30) viewed 1 to 2 therapy activities, and 37% (11/30) did not view any therapy activities. Half of the onboarded young people (15/30, 50%) began a therapy journey, whereas 40% (12/30) of the participants completed at least 1 journey component (ie, therapy activity within a therapy journey), 20% (6/30) completed 2 to 7 journey components, and 20% (6/30) completed ≥10 journey components (refer to Table 3 for a summary of all therapy engagement metrics).

In terms of social network engagement, it was mandatory for the young people to make an introductory post to the community as part of the onboarding process. However, almost half (14/30, 47%) of the young people made at least 1 additional post or comment, whereas 10% (3/30) of them made 2 additional posts or comments, 20% (6/30) of them made 3 to 5 additional posts or comments, and 17% (5/30) of them made >6 additional posts or comments. Furthermore, 47% (14/30) of the young people reacted to at least 1 post or comment on the social network, whereas 27% (8/30) of them reacted to >1 post or comment (refer to Table 3 for a summary of all therapy engagement metrics).

In relation to exchanging private messages with eOrygen staff using the chat function, 47% (14/30) of the young people sent at least 1 message, whereas 13% (4/30) of them sent 1 to 2 messages, 13% (4/30) of them sent 3 to 6 messages, and 20% (6/30) of them sent ≥10 messages. By contrast, 97% (29/30) of the young people received at least 1 private chat message from a clinician or peer worker, whereas 37% (11/30) of them received 1 to 3 messages, 37% (11/30) of them received 4 to 9 messages, and 23% (7/30) of them received ≥14 messages (refer to Table 3 for a summary of these metrics).

a EPPIC: Early Psychosis Prevention and Intervention Centre.

b HYPE: Helping Young People Early.

Qualitative Findings

A thematic analysis of the interviews with the young people was conducted, regarding their experiences with eOrygen, with the aim of identifying facilitators and barriers to their engagement with the platform ( Table 4 ). Facilitators included clinician endorsement, which increased trust in the platform; the presence of peer support workers, fostering a sense of safety and support; a sense of community and connection with other users; personalized therapy content recommended by clinicians; the use of eOrygen for between-sessions work, supported by follow-up discussions; and an easy-to-use interface. Conversely, barriers to engagement included general low motivation, social anxiety hindering social interactions, privacy concerns, inflexible progression in modules, and periods of limited content and interactions on the platform. Addressing these barriers and leveraging the facilitators can enhance the platform’s appeal and effectiveness for a broader range of users seeking mental health support.

The analysis of the clinician focus group grounded in the CFIR identified various barriers and facilitators to the successful implementation and use of the eOrygen intervention ( Table 5 ). Among the notable barriers were the length of the onboarding process for young people, a need for increased confidence in using the platform, and a perceived lack of practical knowledge regarding its features and how these features are related to benefits for young people; in addition, competing priorities, such as addressing risk and acute presentations amid understaffing, consistently disrupted platform use. Conversely, the platform’s positive reputation and alignment with evidence-based frameworks emerged as facilitators. In addition, the ability to access trustworthy content was highlighted as advantageous for clinicians. These findings underscore the multifaceted nature of implementing digital mental health resources and the importance of addressing both barriers and facilitators to optimize their effectiveness.

Principal Findings

To the best of our knowledge, this was the first study to test an integrated blended model of care for youth psychosis and BPD in young people aged 15 to 25 years. The results of this study showed that eOrygen was feasible, acceptable, and safe. In terms of feasibility, we anticipated recruiting approximately 25 clinicians and 1 to 2 young people per clinician to the intervention and expected that the refusal rate would be <50%. Our refusal rate was 25% (15/59), which indicated 1 element of feasibility. We sought to recruit 25 clinicians; the final number of clinicians enrolled in the study was 18 (78%). In addition, we recruited 33 young people (which exceeded our goal) to the study over a 4-month period. Although we did not meet our clinician goal, our recruitment took place at the beginning of the COVID-19 pandemic, which proved a difficult period to introduce a new digital intervention to YMH services and to train clinicians in the use of a new digital platform. Despite these challenges, we still recruited a relatively high percentage of clinicians to the study and exceeded our goal in recruiting young people.

In terms of acceptability, 92% (22/24) of the young people onboarded reported that they would recommend eOrygen to others, exceeding our goal of 90%. Furthermore, 40% (12/30) of the participants used the platform at least once per fortnight during the initial 6 weeks of the intervention period, although only 20% (6/30) maintained fortnightly access across the entire 12 weeks. These findings compare well with another study reporting decreased engagement over time, with retention rates of only 3.9% over 15 days and 3.3% over 30 days for the use of mental health apps in the general population [ 84 ]. Although engagement was strong during the first 6 weeks, more strategies are needed to sustain engagement over longer periods. We did not use any strategies in this pilot to promote young people’s or clinicians’ engagement and left this to the discretion of the participating clinicians because it was purely an ecological study. Therefore, future studies should implement scalable strategies to sustain engagement for clinicians and young people, such as external support, coaching, and automated prompts or reminders.

Higher engagement rates with eOrygen were also observed for young people attending EPPIC (mean 10.4, SD 8.6 active days) versus those attending the HYPE Clinic (mean 6.3, SD 5.7 active days). To the best of our knowledge, this was the first blended model tested for young people with BPD. The MOST model was originally developed and optimized for young people with first-episode psychosis [ 57 , 60 , 85 ]. Therefore, lower engagement rates for young people attending the HYPE Clinic could be because the therapeutic model used by clinicians in face-to-face care was slightly different than the content in eOrygen, and the MOST model may need further refinement and optimization for young people with BPD. Research has indicated that young people with BPD are difficult to engage in face-to-face treatment [ 86 - 88 ], and it is possible that this extends to digital mental health care.

In terms of safety, there were no unlawful entries recorded on the web-based platform, no serious adverse events were experienced by participants, and there was no worsening of clinical or social outcome measures during the intervention. We also anticipated that at least 95% of young people would report feeling safe using the platform, and this goal was exceeded with 96% of the participants reporting feeling safe. Our primary findings are also in line with a previous pilot study testing Orygen Digital’s MOST platform with real-time clinician-delivered web chat counseling, which found that all acceptability and safety indicators exceeded their a priori established criteria [ 59 ].

The secondary outcome variables showed significant pre-post improvements in 9 (75%) of the 12 outcomes assessed. These included borderline symptoms, depression, loneliness, social isolation, social anxiety, stress, psychological distress, social and occupational functioning, and the therapist-reported working alliance. It is important to note that although our study included 2 clinical sites treating young people with complex mental health disorders (eg, psychotic disorders and BPD), there were no significant differences between the sites on outcome variables at baseline. Therefore, improvements in clinical outcomes relate to all participants in the study. The findings also support a previous pilot study (MOST+) that integrated MOST with real-time clinician-delivered web chat counseling [ 59 ]. MOST+ also found statistically significant improvements in psychological distress, depression, and stress. However, both studies are single-group pilot studies, and we cannot make causal inferences from the findings because it cannot be determined from uncontrolled studies whether the observed effects are related to the intervention or to external factors such as individual or in-person treatment characteristics. Future research should confirm these findings by conducting controlled studies with larger sample sizes and greater power.

Findings from a recent qualitative study also suggested that blended care has the potential to enhance the therapeutic relationship [ 40 ]. The study suggested that the TA developed through blended care can enhance engagement with both face-to-face and web-based treatment modalities by offering treatment continuity and personalization as well as enhancing therapeutic intensity, which are key areas of concern in the field [ 24 , 40 ]. In our study, we observed statistically significant improvements for therapist-reported TA but no improvements in client-reported TA. Research has also indicated that TA has moderate but reliable correlations with mental health outcomes [ 89 - 91 ]. Although we observed improvements in therapist-rated TA, they did not correlate with improvements in clinical outcomes; therefore, future research should further explore this, along with the importance of client-rated TA in relation to outcomes.

By contrast, qualitative feedback from participants in our study indicated that eOrygen was beneficial when used in a blended way; for example, young people found it helpful when their clinician recommended content to them that aligned with their in-session work, and they also found the homework to be completed on the eOrygen platform to be helpful for between-sessions work. These findings are in line with other research indicating that blended care is beneficial when it is integrated and intensifies treatment [ 92 ]. However, research has indicated that blended care may not be effective if perceived as burdensome or time consuming by clinicians, but this may be related to trial-related factors, such as reporting to a research team if using the intervention during a clinical trial or inflexible intervention structure [ 93 ]. One way to overcome this could be for developers to work with clinicians to ensure suitable content and for features to be provided within the intervention, which would enable clinicians to use the intervention with young people in a way that is meaningful, relevant, and related to the face-to-face treatment they provide [ 94 ].

Limitations

A number of limitations should be noted. The single-group design was chosen to enhance external validity by maximizing real-world uptake of the intervention. Therefore, it was important to expose as many young people and clinicians to the intervention as possible to determine real-world uptake with eOrygen, and the inclusion of a control group may have negatively impacted the number of clinicians and young people who signed up to the intervention, potentially limiting our understanding of feasibility in this context. However, this study design limited our ability to determine a cause-and-effect relationship between the intervention and outcomes [ 95 ]. Furthermore, a 3-month time frame was chosen because this is an acceptable time frame that is comparable to the time frames of other pilot studies testing the feasibility, safety, and acceptability of digital interventions [ 59 , 66 , 96 ].

Although this study tested an integrated blended model of care, we did not collect data on how young people engaged with face-to-face treatment or how participating clinicians used the eOrygen platform, and future studies should consider this when evaluating blended models of care. Furthermore, our goal to provide flexibility and autonomy to clinicians may have negatively impacted competence in the use of the platform; for example, clinicians attended a 1-day workshop and received a printed user manual and training videos on how to use the eOrygen platform. However, as noted in the clinician-identified barriers to implementation, attending 1 workshop may be inadequate to gain competence, and there was also a substantial gap in time between clinician training and the implementation of eOrygen owing to the COVID-19 pandemic. Therefore, the training may have been forgotten, and a lack of time to review training materials may have also been an issue. Future studies should consider providing ongoing clinician support in this regard, while also remaining flexible to the needs of clinicians. Furthermore, although the recruitment goal was met for this study, it must be noted that the sample of male participants in the study was small at only 21% (7/33) of the total sample, limiting the generalizability of these findings and highlighting that significant barriers may still exist for young men to access mental health treatment [ 97 ] and that difficulties may also exist in tailoring interventions to young men [ 98 ].

Conclusions

In conclusion, our pilot study was an important first step in testing a transdiagnostic blended model of care for youth psychosis and BPD in young people aged 15 to 25 years. We found that eOrygen was feasible, acceptable, and safe; there were indications that eOrygen may improve treatment outcomes if tested in a full-powered trial; and the majority of participants and clinicians reported positive experiences of using eOrygen as a blended model of care. However, some participants misunderstood the meaning of blended care, and future research should ensure that this is clearly outlined before integrating a digital tool into clinical practice. Furthermore, some clinicians reported a lack of knowledge and confidence in their ability to implement the intervention, and future research should aim to understand the possible barriers and address them to ensure clinician competence and confidence with the intervention itself. Overall, this pilot study provides promise for integrating blended models of care into specialized services for young people with complex mental health conditions, but a full-scale trial will be needed to test the effectiveness of such an intervention. This study also reaffirms prior findings indicating that blended models of care have the potential to increase therapeutic intensity, continuity, engagement, and effectiveness. Future research needs to focus on the development of tools to integrate blended care into practice specifically [ 36 ], as well as strategies to support both clinicians and young people in continuous use of the platform.

Acknowledgments

The authors would like to thank the young people who participated in the eOrygen pilot study and agreed to share their data for research purposes. The study was funded by generous support from the Telstra Foundation. MA-J was supported by an investigator grant (APP1177235) from the National Health and Medical Research Council and a Dame Kate Campbell Fellowship from The University of Melbourne. JN was supported by a National Health and Medical Research Council Emerging Leader Fellowship (ID 2009782).

Conflicts of Interest

None declared.

Descriptive insights into the participants’ willingness to use eOrygen again, whether they would recommend it to others, and their initial reasons of interest in using eOrygen.

Young people’s satisfaction with eOrygen (n=25).

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Abbreviations

Edited by J Torous; submitted 22.05.23; peer-reviewed by L Balcombe, X Zhang, M Cederberg; comments to author 29.06.23; revised version received 05.12.23; accepted 12.01.24; published 01.04.24.

©Shaunagh O'Sullivan, Carla McEnery, Daniela Cagliarini, Jordan D X Hinton, Lee Valentine, Jennifer Nicholas, Nicola A Chen, Emily Castagnini, Jacqueline Lester, Esta Kanellopoulos, Simon D'Alfonso, John F Gleeson, Mario Alvarez-Jimenez. Originally published in JMIR Mental Health (https://mental.jmir.org), 01.04.2024.

This is an open-access article distributed under the terms of the Creative Commons Attribution License (https://creativecommons.org/licenses/by/4.0/), which permits unrestricted use, distribution, and reproduction in any medium, provided the original work, first published in JMIR Mental Health, is properly cited. The complete bibliographic information, a link to the original publication on https://mental.jmir.org/, as well as this copyright and license information must be included.

ORIGINAL RESEARCH article

People with newly diagnosed multiple sclerosis benefit from a complex preventative intervention -a single group prospective study with follow up.

• 1 Charles University, Prague, Czechia
• 2 Faculty of Environmental Sciences, Czech University of Life Sciences Prague, Prague 6, Prague, Czechia
• 3 MS Research, Treatment and Education, The Vassall Centre, Bristol, United Kingdom
• 4 Department of Steroids and Proteofactors, Institute of Endocrionology, Prague, Czechia
• 5 Third Faculty of Medicine, Charles University, Prague, Prague, Czechia
• 6 Rehabilitation Clinic Malvazinky, Praha, Czechia

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BACKGROUND: Newly diagnosed people with multiple sclerosis frequently report fatigue, pain, depression and anxiety. Preventative programmes may be beneficial, but there is limited evidence of their effectiveness, especially long-term follow-up. METHODS: The programme consisted of 6-months face to face intervention (an introductory workshop, psychology-led group sessions and individual physical therapy) followed by 6-months self-guided therapy. Outcome measures were taken at baseline, 6 and 12 months. Primary outcomes measures were self-report questionnaires for fatigue, satisfaction with life and disease acceptance. Secondary outcomes were spirometry, spiroergometric parameters and neuroactive steroid levels. RESULTS: From 22 participants enrolled, 17 completed the first six months and 13 the follow-up. Fatigue measured on the Fatigue scale for motor and cognitive functions decreased significantly at six months (p=0.035) and at follow-up (p=0.007). The Modified Fatigue Impact Scale (p= 0.035) and Satisfaction With Life Scale (p=0.007) significantly increased at follow-up. Spirometry, spiroergometric parameters, steroid hormones and neuroactive steroids levels did not change significantly. CONCLUSIONS: This program reduces fatigue and improves satisfaction with life in this patient group with improvements sustained at 12 months. People who participated more frequently showed greater benefit. CLINICAL REHABILITATION IMPACT: The paper describes the effects of a complex preventative intervention for people with newly diagnosed Multiple Sclerosis. The study found that this programme reduces fatigue and improves satisfaction with life with long-term benefit (at 12-month follow up). The individuals who participated less frequently experienced fewer benefits.

Keywords: Multiple Sclerosis, Fatigue, satisfaction with life, cognitive behavioural therapy, Physical Therapy, aerobic training, Neuroactive steroids

Received: 19 Jan 2024; Accepted: 25 Mar 2024.

Copyright: © 2024 Hruškova, Berchová Bímová, Davies Smith, Škodová, Bičíková, Kolatorova, Stetkarova, Krivá, Javůrková, Angelová and Rasova. This is an open-access article distributed under the terms of the Creative Commons Attribution License (CC BY) . The use, distribution or reproduction in other forums is permitted, provided the original author(s) or licensor are credited and that the original publication in this journal is cited, in accordance with accepted academic practice. No use, distribution or reproduction is permitted which does not comply with these terms.

* Correspondence: Kamila Rasova, Charles University, Prague, Czechia

Disclaimer: All claims expressed in this article are solely those of the authors and do not necessarily represent those of their affiliated organizations, or those of the publisher, the editors and the reviewers. Any product that may be evaluated in this article or claim that may be made by its manufacturer is not guaranteed or endorsed by the publisher.

• Open access
• Published: 01 April 2024

Noninvasive spinal stimulation improves walking in chronic stroke survivors: a proof-of-concept case series

• Yaejin Moon 1 , 2 , 3   na1 ,
• Chen Yang 1 , 2   na1 ,
• Nicole C. Veit 1 , 4   na1 ,
• Kelly A. McKenzie 1 ,
• Jay Kim 1 ,
• Shreya Aalla 1 ,
• Lindsey Yingling 1 ,
• Kristine Buchler 1 ,
• Jasmine Hunt 1 ,
• Sophia Jenz 2 ,
• Sung Yul Shin 1 , 2 ,
• Ameen Kishta 1 ,
• V. Reggie Edgerton 5 , 6 ,
• Yury P. Gerasimenko 7 , 8 ,
• Elliot J. Roth 1 , 2 ,
• Richard L. Lieber 1 , 2 , 9 &
• Arun Jayaraman   ORCID: orcid.org/0000-0002-9302-6693 1 , 2  

BioMedical Engineering OnLine volume  23 , Article number:  38 ( 2024 ) Cite this article

Metrics details

After stroke, restoring safe, independent, and efficient walking is a top rehabilitation priority. However, in nearly 70% of stroke survivors asymmetrical walking patterns and reduced walking speed persist. This case series study aims to investigate the effectiveness of transcutaneous spinal cord stimulation (tSCS) in enhancing walking ability of persons with chronic stroke.

Eight participants with hemiparesis after a single, chronic stroke were enrolled. Each participant was assigned to either the Stim group ( N  = 4, gait training + tSCS) or Control group ( N  = 4, gait training alone). Each participant in the Stim group was matched to a participant in the Control group based on age, time since stroke, and self-selected gait speed. For the Stim group, tSCS was delivered during gait training via electrodes placed on the skin between the spinous processes of C5–C6, T11–T12, and L1–L2. Both groups received 24 sessions of gait training over 8 weeks with a physical therapist providing verbal cueing for improved gait symmetry. Gait speed (measured from 10 m walk test), endurance (measured from 6 min walk test), spatiotemporal gait symmetries (step length and swing time), as well as the neurophysiological outcomes (muscle synergy, resting motor thresholds via spinal motor evoked responses) were collected without tSCS at baseline, completion, and 3 month follow-up.

All four Stim participants sustained spatiotemporal symmetry improvements at the 3 month follow-up (step length: 17.7%, swing time: 10.1%) compared to the Control group (step length: 1.1%, swing time 3.6%). Additionally, 3 of 4 Stim participants showed increased number of muscle synergies and/or lowered resting motor thresholds compared to the Control group.

Conclusions

This study provides promising preliminary evidence that using tSCS as a therapeutic catalyst to gait training may increase the efficacy of gait rehabilitation in individuals with chronic stroke.

Trial registration NCT03714282 (clinicaltrials.gov), registration date: 2018-10-18.

Stroke is the leading cause of adult-onset disability [ 1 ]. Despite many advances in gait research in the last decade, about 35% of stroke survivors fail to regain independence in performing activities of daily living due to the impaired function of their affected leg, and about 70% have gait deficits, including reduced walking speeds, asymmetrical walking patterns, and motor coordination issues [ 2 , 3 , 4 ].

Walking deficits after stroke mostly derive from a disruption of the corticospinal pathways that play an important role in transmitting sensory–motor commands [ 5 , 6 ]. To address this, most interventions using non-invasive electrical pulses focus on stimulation of the motor cortex to activate dormant or new pathways [ 2 , 7 , 8 ]. However, while supra-spinal regions can facilitate fine locomotor control, spinal networks ultimately generate the basic locomotor pattern [ 9 , 10 ]. More interestingly, a recent study using functional MRI showed increased blood-oxygen-level dependent activities in motor cortex following transcutaneous spinal cord stimulation (tSCS) in individuals with stroke [ 11 ]. Therefore, we hypothesized that tSCS would facilitate an improvement of gait after stroke. Our previous work, in collaboration with additional researchers, established anatomical and physiological changes in the spinal cord after stroke [ 12 , 13 ], offering a theoretical basis for testing our hypothesis of targeting the spinal circuits for post-stroke recovery.

Recently, Moshonkina et al. reported functional improvements in post-stroke individuals after 2 weeks of tSCS with standard physical therapy, achieving the minimum clinical important differences (MCID) in the 6 min walk test and comfortable walking speed [ 14 ]. The same investigators reported immediate improvements in walking kinematics after a single tSCS session [ 15 , 16 ]. Notably, however, none of the studies mentioned above investigated the effects of more than 4 weeks of training nor tried to explore the potential neurophysiological differences accompanied with gait outcomes. Consequently, it remains unclear whether tSCS can exert a lasting impact on restoration of function following a stroke.

We investigated whether tSCS combined with symmetry-focused gait training has a sustained effect on gait recovery after chronic stroke. We hypothesized that longer-term gait training (24 sessions) with tSCS would lead to greater sustained improvements in walking function compared to control treatment focused solely on gait training. Specifically, we focused on gait symmetry since such improvements can have lasting effects on balance and overall mobility of stroke survivors [ 6 ]. We also expected that gait improvements would be associated with physiological changes in muscle coordination measured from electromyography (EMG) of the paretic side, and spinal excitability determined by the spinal motor evoked responses (sMERs).

Spatiotemporal symmetry

After 24 sessions of training, all four stroke participants that received stimulation (Stim group) improved step length symmetry at post training (Post) compared to before training (Pre) (20.0 increase in absolute symmetry index; 95% Confidence Intervals (CIs): [3.6–36.3]; P  = 0.05). In contrast, in the control group, only Control 3 showed improved step length symmetry (33% increase), which was lower than that of the matched Stim participant (Stim 3: 64% increase). For swing time symmetry, all Stim participants except Stim 3 showed improvements (9.9 increase; 95% CIs [3.5–17.1]; P  = 0.05), while all controls showed no changes in swing time symmetry (−0.1 change; 95% CIs [−0.8–0.7]; P  = 0.39).

At the 3-month follow-up (3FU) assessment, all Stim participants continued to demonstrate improved step length symmetry (17.7 increase; 95% CIs [2.3–33.1]; P  = 0.05) and swing time symmetry (10.1 increase; 95% CIs [5.8–14.5]; P  = 0.04) compared to before training. The symmetry from Post to 3FU did not change significantly for the Stim participants (step length symmetry: −2.2 decrease, 95% CIs [−4.8–0.7], P  = 0.10; swing time symmetry: 0.2 increase, 95% CIs [−8.1–8.0], P  = 0.46), nor the Control participants (step length symmetry: 0.9 increase, 95% CIs [−0.7–2.6], P  = 0.22; swing time symmetry: 3.7 increase, 95% CIs [1.9–6.5], P  = 0.15), Furthermore, all four Stim participants exhibited a greater degree of improvement at the follow-up assessment relative to their Pre, surpassing the level of increases observed in the matched Control participants (Table  1 ). The Control group did not show significant Pre-3FU changes (step length symmetry: 1.1%; 95% CIs [−7.4–12.8]; P  = 0.45; swing time symmetry : 3.6%; 95% CIs [1.4–6.9]; P  = 0.16). Step length and swing time symmetries of each participant at Pre, Post, and 3FU are reported in Tables  1 , 2 .

At Post, all Stim participants increased their fast-walking speed (0.33 ± 0.21 m/s increase), which exceeded the MCID of 0.14 m/s. In contrast, only Control 1 met the MCID (0.14 m/s increase) but as a group, the control group did not meet the MCID (0.05 ± 0.08 m/s increase).

At 3FU, two participants (Stim 2, 3) from the Stim group maintained their fast-walking speed over MCID when compared to Pre (Stim 2: 0.14 m/s increase; Stim 3: 0.19 m/s increase), while one Control participant managed to maintain such an improvement (Control 4: 0.22 m/s increase). From Post to 3FU, three Stim participants (Stim 1, 3, and 4) decreased their speed beyond the MCID, with Stim 1 and 4 returning to baseline speed and Stim 3 maintaining a fast-walking speed over the MCID. Table 3 shows the measured speeds and corresponding percent changes from Pre to Post and 3FU, and Post to 3FU for all participants.

6-min walk test (6MWT)

All Stim participants increased their 6MWT distance (61.6 ± 42.8 m increase) at Post over the MCID of 34.4 m. In contrast, only Control 2 had improvements over the MCID (43.7 m increase), with the matched Stim participant experiencing greater improvements (Stim 2: 49.3 m increase). The Control group had an average improvement of 25.8 ± 13.3 m.

At 3FU, only one participant from each group maintained a walking distance over the MCID compared to before training (Stim 1: 45.0 m increase, Control 4: 58.1 m increase). All participants, except Control 4, decreased their walking distance from Post to 3FU. Table 4 shows the raw data and percent changes from Pre to Post and 3FU, and Post to 3FU for each participant.

Muscle synergy analysis during walking

Muscle synergies indicate synchronous neural commands to execute each phase of gait cycle and the group of muscles that are activated together in response to a neural command [ 17 ]. The number of muscle synergies measured from electromyography (EMG) in the paretic side was compared between Pre and Post assessments. Two Stim participants (Stim 1–4) increased the number of synergies after the intervention, which has been considered as an indication of improved neuromuscular coordination after stroke [ 18 ]. None of the Control participants showed an increase. For Stim 1, the number of synergies increased from two to three (Fig.  1 A). Specifically, at Post, an additional synergy was observed with a dominant activity in vastus lateralis (VL) during loading phase (synergy 3 in Fig.  1 A Post). For Stim 4, a single synergy was observed at the baseline with a strong response at stance phase (Fig.  1 B Pre). At Post, an extra synergy was present in late stance and swing phase with a dominant activation at medial hamstring (MH) and medial gastrocnemius (MG) muscles (synergy 2 in Fig.  1 B Post).

Muscle synergy analysis results. Muscle synergy weightings and synergy activation pattern profiles of the Stim participants with increased number of muscle synergies Post-intervention ( A : Stim 1, B : Stim 4). Vertical dashed line indicates toe off timing. TA tibialis anterior, MG medial gastrocnemius, VL vastus lateralis, RF rectus femoris, MH medial hamstring

Resting motor threshold (RMT)

Two participants in the Stim group exhibited a decrease in Post-intervention RMTs compared to Pre-intervention in tibialis anterior (TA) (Fig.  2 ; Stim 2: 24%, Stim 4: 17% decrease) and medial gastrocnemius (MG) (Stim 2: 44%, Stim 4: 21% decrease) (refer to Additional file 1 : Table S1). Notably, these participants had the highest RMT levels at baseline. All other participants exhibited minimal Pre–Post changes in RMTs (≤ 10 mA), with no significant changes from Pre to Post on average (Stim TA: −14 mA, 95% CIs [−33–5], P  = 0.14; Stim MG: −30 mA, 95% CIs [−66–0], P  = 0.12; Control TA: −3 mA, 95% CIs [−3–3], P  = 0.17; Control MG: 0 mA, 95% CIs [0–5], P  = 0.50). Control 2 did not demonstrate any spinal motor evoked responses (sMERs).

Spinal motor evoked responses (sMERs) results. A The responses recorded at Pre and Post-intervention of Stim 2 in the TA and MG muscles of the paretic leg at stimulation intensities at L1 ranging from 50 to 180 mA (5 mA increments). Notably, both muscles responded at lower stimulation intensity (i.e., reduced RMT) at Post compared to Pre-intervention indicating improved spinal excitability. B , C Individual (line graph; identified by ID within groups) Pre–Post RMT changes for B TA muscle and C MG muscle. RMT resting motor threshold, TA tibialis anterior, MG medial gastrocnemius

Participants’ self-report

None of the participants experienced self-reported pain or discomfort during or following the protocol. Informal reports on the effects of the intervention from subjects in the Stim group included: “It has helped me with the stairs and engaging my core in a dynamic way”, “Walking around my house without my cane has gotten a lot better” and “My standing and walking without my brace has gotten better”. Stim group subjects also described improvements in proprioception: “I feel my feet,” and “I feel more aware of my leg after starting this.” None of the participants in the control group provided explicit indications of intervention effects.

In this case series study, we present preliminary evidence that tSCS applied during gait training enhances walking ability, demonstrating increases in spatiotemporal gait symmetry and clinically meaningful improvements in gait speed and walking distance after 24 sessions in individuals with chronic stroke. The clinical findings were accompanied by selected neurophysiological changes.

Our study revealed that all participants in the Stim group maintained or improved step length and swing time symmetry at Post training. Additionally, improvements over the MCID were seen for all four Stim participants for both, 6MWT and fast gait speed, at Post training, however, most participants did not retain the improvements from Post to 3FU and went back to baseline level (except Stim 1 in 6MWT, and Stim 2 and 3 in gait speed). This suggests tSCS might boost the initial endurance and speed improvements when combined with gait training but may be reversed to baseline levels if exercise is discontinued. In contrast, at 3FU, the Stim group continued to maintain a better spatiotemporal symmetry compared to Pre. Such positive gait symmetry changes have been linked with an increased quality of life due to better balance, reduced fall risks, and increased independence as individuals could better reintegrate into the community [ 6 , 19 ]. These observations support the hypothesis that tSCS paired with gait training focused on gait symmetry facilitates improved gait performance and walking patterns following the intervention. However, this comprehensive improvement in gait function disappeared at 3FU, showing only lasting improvement in gait symmetry.

Notably, we observed a variety of patterns for symmetry improvement within the stimulation group. Specifically, Stim 1 and Stim 3 demonstrated improved step length symmetry (74%–64%), while Stim 2 and Stim 4 exhibited improvements in swing time symmetry (37%–9%). These patterns seemed to be linked to the individuals’ baseline gait symmetry, with more substantial improvements observed in metrics with greater deficits. Importantly, the improvements in one aspect of symmetry were not at the sacrifice of other symmetry metrics for any of the Stim participants. This finding highlights the importance of providing individualized training instructions and stimulation parameters to maximize the effect of tSCS in future studies aimed at enhancing activity-dependent learning.

To probe the underlying neuromuscular changes associated to gait performance after the intervention, we conducted muscle synergy analysis to evaluate neural activity during movement and sMERs to explore the changes in excitability at the local spinal networks. In our study, the two Stim participants (Stim 1–4) who demonstrated an increased number of muscle synergies had the greatest improvements of spatiotemporal symmetry at their 3FU, which is aligns to the findings by Clark et al. suggesting the number of muscle synergies is positively correlated with step length symmetry [ 18 ]. Additionally, not only the number of synergies increased, but also the structure of the new synergies reflected those found in healthy locomotion. For Stim 1, Synergy 1 at baseline unmerged into two separate synergies: Synergy 1 with dominant activity in VL for early stance and Synergy 3 with dominant activity in MH for early swing, which is consistent on what is found in healthy locomotion [ 20 ]. This observation, combined with earlier studies indicating the involvement of local spinal networks in muscle synergies activation [ 21 , 22 ], indicates that tSCS may fine-tune muscle activation patterns that could lead to sustained improvements in motor behaviors. Hence, we propose that tSCS might be a viable approach for altering muscle synergies in stroke and therefore targeting the underlying gait deficits of this population.

Additionally, in the sMERs test, two Stim participants (Stim 2–4), who had the highest baseline RMTs, exhibited a substantial decrease in RMT Post-intervention whereas all Control participants showed only minimal changes. This decreased RMT suggests an enhancement in the participants’ spinal excitability after training, a finding in line with earlier studies on tSCS [ 23 , 24 , 25 , 26 ]. These previous studies demonstrated that tSCS appears to prime spared spinal networks and increase net excitability [ 27 , 28 , 29 ] allowing supra-spinal and peripheral inputs to exceed the motor thresholds needed to generate voluntary movement [ 28 ]. It has been suggested that the stimulation may reorganize the cortico-reticulo-spinal circuits through this convergence between residual supra-spinal commands and activated afferent pathways, potentially accounting for the persistent motor recovery even in the absence of stimulation [ 25 , 30 ]. However, these findings lack generalizability since the changes were seen only in some Stim participants. Future research is required to elucidate the significance of spinal cord RMTs within the context of stroke pathology.

A larger sample size is warranted to understand how neurophysiological and functional outcomes after tSCS are correlated and how the changes in spinal excitability are linked to stroke recovery. A post hoc calculation, based on our primary outcome of spatiotemporal gait symmetry, indicated that a total of 50 participants (25 in each group) are required to provide 80% power at a two-sided 5% significance level. Furthermore, the tSCS stimulation parameters used were primarily based on therapist observation, potentially contributing to the observed between-subject variability in outcomes at both Post and 3FU. Additionally, while the pairs were matched as best as possible, our pairs were not matched based on our primary outcome measure (symmetry). This underscores the necessity for personalized tSCS, where stimulation parameters can be tailored to address each individual’s specific gait deficit. Notably, Bogacheva et al. (2023) have employed a gait phase-dependent tSCS stimulation protocol in stroke survivors [ 15 ]. This protocol alters the stimulation site based on the gait phase, with stimulation at the T12 vertebrae during the swing phase and at the L1 vertebrae during the stance phase. Nonetheless, the study assessed the effect of stimulation in only a single session intervention. For future studies, we could combine our approach—which provides extended gait training combined with tSCS—with the phase-dependent tSCS stimulation protocol to target improvements in individual-specific gait deficits. However, a more in-depth understanding of stimulation parameters is crucial before conducting accurate personalized tSCS interventions. In summary, the promising preliminary results of this study portend a significant effect when the upcoming clinical trial (HD106015, Clinical Trials Number: NCT05167786) is completed ( n  = 50).

In summary, this pilot case series successfully demonstrates the feasibility and potential benefit of implementing tSCS in combination with symmetry-focused gait training for individuals with chronic stroke. Our findings suggest that further research is warranted to unlock the potential of tSCS as a neuromodulation technique aimed at improving function in individuals post-stroke.

Study design, setting, and participants

This two-arm, unblinded, pilot case series study was conducted from 2018 through 2020 at Shirley Ryan AbilityLab in Chicago, Illinois. The trial protocol was approved by the institutional review board at Northwestern University. All participants provided written informed consent. Northwestern University Institutional Review Board (IRB) approved this study (IRB protocol #00206430). The study design and conduct complied with all relevant regulations regarding the use of human study participants and was conducted in accordance with the criteria set by the Declaration of Helsinki. The trial protocol was preregistered at ClinicalTrials.gov (NCT03714282).

The participants in this study were recruited by convenience sampling from the Shirley Ryan AbilityLab. Participant inclusion criteria included the following: age over 18 years, at least 1 year post-stroke, hemiplegia secondary to a single stroke, Functional Ambulation Category of 2 or greater, able to provide informed consent, not currently receiving physical therapy services, not participating another clinical trial at the time of the intervention and in the months prior to, and physician approval. Participant exclusion criteria were the following: ataxia, multiple stroke history, currently taking a Selective Serotonin Reuptake Inhibitor or Tricyclic Antidepressant, botulinum toxin injection in the lower extremity within the last 4 months, Modified Ashworth Scale of 3 or greater in the lower extremity, pregnancy or nursing, presence of pacemaker, active pressure sores, unhealed bone fractures, peripheral neuropathies, painful musculoskeletal dysfunction due to active injuries or infections, severe contractures, medical illness limiting ability to walk, active urinary tract infection, clinically significant depression, psychiatric disorders or ongoing drug abuse, metal implants in spine, history of cancer or cancer remission < 5 years.

Eight participants were assigned to either the Stim group ( N  = 4, tSCS + gait training) or Control group ( N  = 4, gait training alone). To minimize possible confounding factors, each Stim group participant was matched to a Control participant for age (± 3 years), time since stroke (± 3 years), and self-selected gait speed (± 0.14 m/s, based on MCID [ 31 ]) (Table  5 ). All subjects were able to ambulate without any hand support.

Study protocol

Participants completed 45 min of gait training, 3 times per week, for 8 weeks for a total of 24 sessions with a primary focus on improving spatiotemporal gait symmetry. The Stim group received tSCS during gait training while the Control group received gait training only. Gait performance outcomes were assessed at 3 timepoints: before training (Pre), after all training sessions (Post), and in a 3 month follow-up after the last training session (3FU). All gait assessments were completed without tSCS. Neurophysiological measures were also assessed at Pre and Post timepoints to explore the underlying neurophysiological variations contributing to gait performance changes.

Gait training protocol

During training sessions, all participants completed locomotor training in three positions: side-lying (10–15 min), treadmill (25 min), and overground (5–10 min) (Fig.  3 A). The side-lying training was intended to train rhythmic and symmetrical lower-limb movements in a gravity neutral position as participants laid on their non-paretic side (Fig.  3 B) [ 32 , 33 ]. Treadmill locomotion was performed on a treadmill (C-Mill ® , Motek Medical) that provided real-time feedback on spatiotemporal gait parameters. Participants then transitioned to overground locomotion to promote functional carryover. As training sessions progressed, participants spent less time in side-lying training and more time on overground ambulation. All the gait training was conducted with a licensed physical therapist. The physical therapist provided verbal cue for spatiotemporal symmetry in both overground and treadmill trainings. For treadmill sessions, the participants were encouraged not to use the handrail but were allowed to hold it for support if necessary.

Study protocol and stimulation setup. A Overall experimental protocol. B Top–down view of position of the legs extended beyond the edge of the table and supported with vertically cables during the side-lying training of a participant (Stim 2). C tSCS delivered using surface electrodes on the skin between the C5–6, T11–12, and L1–2 spinous processes (cathode) and a surface electrode on each anterior crest (anode, not shown). D Schematic representation of biphasic pulse sequence used for tSCS. tSCS transcutaneous spinal cord stimulation, OG overground walking, 10MWT 10-m walk test, 6MWT 6-min walk test

Stimulation settings

A custom-built, constant current, spinal stimulator (BioStim-5, Cosyma, Moscow, Russia) [ 34 ] provided tSCS to the Stim group during gait training. tSCS was delivered via cathode electrodes (3.2 cm diameter, ValuTrode, Axelgaard Ltd., Fallbrook, CA, USA) placed on the skin between the C5–6, T11–12, and L1–2 vertebrae (Fig.  3 C) [ 35 ]. Anode electrodes ( 7.5 × 13 cm, UltraStim, Axelgaard Ltd., Fallbrook, CA, USA) were placed bilaterally on the anterior iliac crests. Stimulation consisted of a continuous, biphasic waveform, cathodic-leading, with rectangular 1-ms pulses (0.5 ms per phase) at 30 Hz, modulated at 5 kHz (Fig.  3 D). Subthreshold stimulation intensities (i.e., below the resting motor threshold) were explored since they are known to be superior to suprathreshold stimulation when targeting improved motor activation in a rat model [ 36 ]. The motor threshold was determined by the spinal motor evoked responses (sMERs) test (see the details at the outcome assessments section). C5–6 was also stimulated as a prior tSCS study reported the addition of C5–6 with stimulation to T11–12 and L1–2 immediately improved non-voluntary stepping performance in participants without neurologic conditions [ 23 ]. The study suggested these sites are consistent with the long propriospinal system modulating the lumbosacral locomotor circuit. For each Stim participant, varying combinations of subthreshold stimulation intensities were assessed during ambulation. For each intensity combination, walking performance was recorded using GAITRite electronic walkway (CIR System Inc., NJ, USA) and through the observational evaluation of physical therapists. The objective was to achieve the most symmetrical gait pattern, as gauged by both GAITRite outcomes (step length and swing time symmetry) and clinical observations. Table 6 lists the intensities of tSCS that were applied at each stimulation location by Participant ID#.

Intervention adherence and tolerability

To monitor the participants’ safety during the tSCS intervention, we documented informal self-reports on whether there was any discomfort or pain during each training session. We also measured heart rate and blood pressure at the start and end of each session to ensure the values were in the normal range. All subjects tolerated and adhered to the training sessions well, with no reported adverse effects.

Outcome assessments

Performance based tests.

Spatiotemporal gait symmetry. Participants walked at their self-selected velocity along the 8 m GAITRite electronic walkway (CIR System Inc., NJ, USA) placed in the middle of a 14 m walkway. Each participant completed three trials to account for trial-to-trial variance, and the results were averaged. For each trial, spatiotemporal gait measurements of step length and swing time were extracted. Gait symmetry, the difference between a subject’s paretic (P) and non-paretic (NP) side, was calculated by the following Symmetry Index equation

This calculation results in a maximum value of 100% irrespective of which limb demonstrates greater values, with improvements observed as positive values [ 37 ]. The symmetry indices of three trials for each participant were averaged.

Fast gait speed. To measure gait speed, participants performed the 10 m walk test (10MWT) at fast velocity [ 38 ]. The test was repeated over 3 trials and the average speed of the three trials was calculated.

6 min walk test (6MWT). The 6MWT was conducted to examine gait endurance. Participants were instructed to complete 6 min of overground walking, covering as much distance as possible [ 39 ].

Neurophysiological outcomes

Electromyography ( EMG) acquisition during walking. Surface EMG (Trigno, Delsys, Inc.) was recorded at Pre and Post in five muscles (rectus femoris, RF; vastus lateralis, VL; medial hamstring, MH; tibialis anterior, TA; and medial gastrocnemius, MG) as participants walked at their self-selected speed for 10 m. All EMG data were collected at 2000 Hz. The selected EMG signals from each participant were band-pass filtered from 40 to 500 Hz with a zero-lag fourth-order Butterworth filter, demeaned, rectified, and low-pass filtered with a zero-lag fourth-order Butterworth filter at 4 Hz [ 18 ]. To facilitate comparison between subjects, the filtered signal was normalized to its peak value and resampled into 100% of the gait cycle from heel strike to heel strike.

Muscle synergy analysis. The concept of muscle synergies indicates synchronous neural commands to execute each phase of gait cycle and the group of muscles that are activated together in response to a neural command [ 17 ]. We conducted non-negative matrix factorization to obtain the EMG-based muscle synergy analysis during walking [ 20 , 40 ]. Muscle activity during walking can be grouped into sets of co-excited muscles, termed as muscle modules or synergies [ 41 ]. Studies have identified well-coordinated gait in healthy individuals can be produced by four or five group of synergies [ 18 , 20 , 42 ]. Recent evidence suggests that disinhibition and/or hyperexcitation of the brainstem descending pathways and intraspinal motor network diffuse spastic synergistic activation post-stroke [ 43 ]. As a result, simplified or merged muscle synergies compared to non-impaired individuals are typically observed and has been found to predict their degree of impairment [ 18 ]. Furthermore, previous studies suggest that muscle synergies are encoded in the spinal cord [ 18 , 21 , 22 , 44 ], therefore we hypothesized that modulating spinal networks with tSCS may lead to positive changes in motor control of stroke survivors that could translate to sustained functional gait changes. Previous research suggested that the increase in number of muscle synergies indicate improvement in neuromodular complexity [ 18 ]. To determine the number of muscle synergies necessary to reconstruct the original EMG signal, the variability accounted for (VAF) was calculated and used as the reconstruction quality criterion given by

where \({{\text{EMG}}}_{{\text{o}}}\) is the original EMG signals, \({{\text{EMG}}}_{{\text{r}}}\) is the reconstructed EMG signals calculated by multiplying muscle group weightings and activation timing patterns [ 18 ]. The number of motor synergies of each walking trial was chosen such that the VAFs exceeded 90% [ 18 ].

Spinal motor evoked responses ( sMERs). Following the methods of our previous work [ 12 ], sMERS were performed as participants laid supine and EMG was recorded bilaterally from the same five muscles used for muscle synergy analysis. Surface EMG activity of sMERs was recorded with pairs of bipolar Ag–AgCl surface electrodes (2.5 cm diameter, GS26, Bio-Medical Instruments, Michigan USA). Stimulation was delivered at L1–2 vertebrate site using monophasic, square-wave, single pulses at 5 mA increments, increasing from 5 to 250 mA or until the subject reached maximum tolerance. Each stimulation intensity was delivered three times. EMG signals were sampled at 4000 Hz and band-pass filtered (fourth-order Bessel filter, 30–2000 Hz) by the PowerLab 16/35 data acquisition system operated with LabChart 7.2 Software (AD Instruments, Australia). Resting motor thresholds (RMTs) were calculated for TA and MG as the lowest current intensity at which two out of the three trials had a peak-to-peak amplitude greater than 0.05 mV [ 45 ]. TA and MG were chosen since they exhibited primary weakness in all participants on the paretic side based on the manual muscle testing. The RMTs are used as a reference for the current intensity to be used with continuous stimulation during the intervention. A reduction in RMT after intervention may indicate increased motoneuron excitability, implying that the motoneurons are more responsive to supra-spinal input [ 12 , 24 ].

Participants self-reports were obtained at the conclusion of the intervention for the Stim group, supplemented by any comments they provided throughout the 8 week intervention period.

Data analysis

Bootstrapping for spatiotemporal symmetry and RMTs. For gait symmetry, bootstrap methods were performed to statistically verify changes in the outcomes Post and at 3FU relative to Pre, and 3FU relative to Post (SPSS v27.0, IBM, Inc., Chicago, IL). Additionally, bootstrap methods were performed to evaluate the changes in RMTs from Pre to Post. Bootstrapping is a nonparametric statistical analysis that employs resampling techniques and has been effectively used in studies with small sample sizes [ 47 ]. Specifically, bootstrapping resamples each original data set with replacement, and recombines it to create bootstrap sets, from which the means and 95% confidence intervals (CIs) were obtained. We constructed 1000 bootstrap samples for each outcome and calculated the Pre–Post, Pre-3FU, and 3FU-Post mean raw symmetry index differences, and the Pre–Post means differences of the RMTs of the resampled data to create statistical results. Then, 95% CIs of the differences were constructed to test the null hypothesis of no difference in the mean. Since we hypothesized that the outcomes would improve in subsequent timepoints, we used a one-tailed paired t-test. The raw changes in spatiotemporal symmetry indexes and RMT changes are presented in the results with 95% CIs and the P- value from the bootstrap. The level of significance was set at P  < 0.05.

Minimum clinical important differences ( MCID) for gait speed and 6MWT. For gait speed and 6MWT, MCID was used to assess for meaningfulness of improvements (gait speed MCID = 0.14 m/s; 6MWT distance MCID = 34.4 m) [ 31 ]. These thresholds are defined as the smallest changes in health-related measures that patients perceive as meaningful improvements in rehabilitation. This approach was chosen over relying solely on statistical significance since a statistically significant change may not always translate into a meaningful improvement in rehabilitation outcomes [ 48 ].

Muscle synergies analysis. The change in number of muscle synergies was reported in the results.

Availability of data and materials

The data and code for analysis used in this paper can be made available upon request.

Abbreviations

Transcutaneous spinal cord stimulation

Minimum clinical important differences

Institutional Review Board

Hemorrhagic

Before training

After all the training sessions

3-Month follow-up after the last training session

10-Meter walk test

6-Minute walk test

Spinal motor evoked responses

Non-paretic

Electromyography

Rectus femoris

Vastus lateralis

Medial hamstring

Tibialis anterior

Medial gastrocnemius

Variability accounted for

Resting motor threshold

Confidence interval

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This study was supported by the Frankel Family Foundation (Julius N. Frankel Foundation).

Author information

Yaejin Moon, Chen Yang and Nicole C. Veit have contributed equally to the manuscript.

Authors and Affiliations

Shirley Ryan AbilityLab, 355 E. Erie St, Chicago, IL, 60611, USA

Yaejin Moon, Chen Yang, Nicole C. Veit, Kelly A. McKenzie, Jay Kim, Shreya Aalla, Lindsey Yingling, Kristine Buchler, Jasmine Hunt, Sung Yul Shin, Ameen Kishta, Elliot J. Roth, Richard L. Lieber & Arun Jayaraman

Feinberg School of Medicine, Northwestern University, Chicago, IL, 60611, USA

Yaejin Moon, Chen Yang, Sophia Jenz, Sung Yul Shin, Elliot J. Roth, Richard L. Lieber & Arun Jayaraman

Department of Exercise Science, Syracuse University, Syracuse, NY, 13057, USA

Yaejin Moon

Biomedical Engineering Department, McCormick School of Engineering, Northwestern University, Evanston, IL, 60208, USA

Nicole C. Veit

Rancho Los Amigos National Rehabilitation Center, Broccoli Impossible-to-Possible Lab, Rancho Research Institute, Downy, CA, 90242, USA

V. Reggie Edgerton

Neurorestoration Center, Keck School of Medicine, University of Southern California, Los Angeles, CA, 90033, USA

Kentucky Spinal Cord Injury Research Center, University of Louisville, Louisville, KY, 40202, USA

Yury P. Gerasimenko

Pavlov Institute of Physiology, St. Petersburg, Russia

Hines VA Medical Center, Maywood, IL, 60141, USA

Richard L. Lieber

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Contributions

Y.M., K.M., L.S., K.B. conducted training sessions. Y.M., K.M., L.S., K.B., J.H., S.J. helped with the collection of data. Y.M., C.Y., N.C.V., J.K., S.A., S.Y.S., A.K. analyzed and interpreted data. V.R.E., Y.P.G., E.J.R., R.L.L., A.J. were involved in the conceptualization of the project and designed study protocol. E.J.R., R.L.L., A.J. acquired the funding. Y.M. wrote the initial draft of the manuscript with C.Y. and N.C.V. and all authors contributed to reviewing and editing the final draft.

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Correspondence to Arun Jayaraman .

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The trial protocol was approved by the institutional review board at Northwestern University. All participants provided written informed consent. Northwestern University Institutional Review Board (IRB) approved this study (IRB protocol #00206430). The study design and conduct complied with all relevant regulations regarding the use of human study participants and was conducted in accordance with the criteria set by the Declaration of Helsinki.

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Written informed consent for publication was obtained from all study participants.

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The authors declare no competing interests.

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Supplementary Information

Additional file 1: table s1.

. Resting motor threshold (RMT, mA) of sMERs of each participant at each assessment and their Pre to Post changes. RMT resting motor threshold, sMER spinally motor evoked responses, TA tibialis anterior, MG medial gastrocnemius.

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Moon, Y., Yang, C., Veit, N.C. et al. Noninvasive spinal stimulation improves walking in chronic stroke survivors: a proof-of-concept case series. BioMed Eng OnLine 23 , 38 (2024). https://doi.org/10.1186/s12938-024-01231-1

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Received : 09 January 2024

Accepted : 21 March 2024

Published : 01 April 2024

DOI : https://doi.org/10.1186/s12938-024-01231-1

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